Supraglottic airway device versus tracheal intubation in the initial airway management of out-of-hospital cardiac arrest: the AIRWAYS-2 cluster RCT

Changes to trial design after commencement of the trial

During the trial, several amendments were made to the trial protocol. For a more detailed description of these amendments, see Appendix 2. The protocol version in use at the start of the trial was version 2.0. The current full trial protocol can be found on the project web page (URL: www.journalslibrary.nihr.ac.uk/programmes/hta/12167102#/; accessed 3 March 2021).

Throughout the trial, adjustments had to be made to the collection of data for the economic evaluation. We aimed from the outset to make use of routinely collected data from NHS Digital Hospital Episode Statistics (HES)/Office for National Statistics (ONS) data linked to the trial cohort. However, as the trial progressed, it became clear that there was a risk that the HES/ONS routine data would take too long to arrive and might not be available in time for the final analyses. The initial application to NHS Digital for the data was made in July 2016. There were various delays to the application process that were beyond the control of the trial team. In late 2017, it was agreed that the trial team would try to acquire a set of routine data by other means so that data would be available should the HES/ONS data not be available in time for analysis. It was agreed with the sponsor (South Western Ambulance Service NHS Foundation Trust) and REC that a sample of sites could be approached and asked to complete brief data collection forms to be used to estimate resource use by collecting information on admissions, cross-sectional imaging [computerised tomography (CT) and magnetic resonance scans] and interventions received by AIRWAYS-2 participants at their sites. In February 2018, a sample of sites was approached to collect this additional retrospective health economics data. A total of 24 hospitals across the four regions were approached, with 18 hospitals returning completed data collection forms for around 850 patients. However, these data were not used in the final analyses because the HES/ONS data became available.

Some changes were made to the statistical analysis plan (SAP) after the trial had started. For a more detailed description of these changes, see Appendix 3. The initial SAP was finalised in February 2018. In April 2018, version 2.0 of the SAP was signed off.

Paramedic population

Paramedics were eligible if they were employed by one of the four participating ambulance services (see Settings) and undertook general operational duties and, therefore, could be despatched to attend an OHCA as the first or second paramedic to arrive at the patient’s side. Paramedics had to be registered with the Health and Care Professions Council (HCPC) and be qualified to practise TI in their clinical role. Paramedics were required to undergo trial-specific training prior to providing consent to participate.

Patient eligibility criteria

The trial population was adults who had a non-traumatic OHCA. Patients were treated in accordance with the allocation of the attending paramedic.

The trial inclusion criteria were:

• patient known or believed to be aged ≥ 18 years

• patient has had a non-traumatic cardiac arrest outside hospital

• patient attended by a paramedic who was participating in the trial and was either the first or second paramedic to arrive at the patient’s side*

• resuscitation was commenced or continued by ambulance staff or responder. ^†

*The participating paramedic managed the patient’s airway according to their allocation. If both the first and second paramedic were participating in the trial, the patient’s airway was managed in accordance with the allocation of the first paramedic to arrive at the patient’s side (usually designated as the ‘attendant’ in the ambulance service). If the first paramedic to arrive was not an AIRWAYS-2 paramedic (i.e. a paramedic who provided consent and was randomised) but the second paramedic was, the patient was enrolled in the trial unless an advanced airway intervention had already occurred (advanced airway intervention being defined as either a SGA or a tracheal tube being present in the patient’s mouth) at the point that the second paramedic arrived at the patient’s side. If a third or subsequent paramedic arrived at the patient’s side, and the first two paramedics were not participating in the trial and the third or subsequent paramedic was participating in the trial, the patient was excluded (some of these exclusions had to be determined retrospectively).

^†Circumstances in which resuscitation should and should not be attempted are described in national guidelines; the Joint Royal Colleges Ambulance Liaison Committee (JRCALC) Recognition of Life Extinct (ROLE) criteria28 are currently used by all ambulance trusts to determine when a resuscitation attempt is inappropriate and these criteria were applied in the trial. These criteria were objectively defined, but the frequency of attempted resuscitation in both groups was examined regularly by the Data Monitoring and Safety Committee (DMSC) to identify any bias in the commencement of resuscitation attempts.

The exclusion criteria were:

• patient detained by Her Majesty’s Prison Service (HMPS)

• patient previously enrolled in the trial (determined retrospectively)

• resuscitation considered inappropriate28

• advanced airway device inserted by another HCPC-registered paramedic, doctor or nurse already in place when the AIRWAYS-2 paramedic arrived at the patient’s side (when the first paramedic to arrive was not participating in the AIRWAYS-2 trial)

• known to already be enrolled in another pre-hospital randomised trial

• mouth opening < 2 cm.

This last exclusion criterion was applied because successful insertion of a SGA requires mouth opening of > 2 cm. There was a risk of post-randomisation bias being introduced by this exclusion criterion, but in our feasibility trial only 2 out of 711 patients (0.3%) were excluded on these grounds. We monitored this exclusion, under the guidance of the DMSC, and had the exclusion rate exceeded 1% we would have taken action to address this through enhanced training and supervision.

Standardised guidelines, based on those produced by the JRCALC, were applied to determine patients for whom a resuscitation attempt was inappropriate. This was the case where there was no chance of survival; where the resuscitation attempt would be futile and distressing for relatives, friends and health-care personnel; and where time and resources would be wasted undertaking such measures.

When any one or more of the following conditions existed, resuscitation and enrolment in the trial would not take place:

• massive cranial and cerebral destruction

• hemicorporectomy

• massive truncal injury incompatible with life (including decapitation)

• decomposition/putrefaction

• incineration

• hypostasis

• rigor mortis

• a valid ‘do not attempt resuscitation’ order or an advanced directive (living will) that states the wish of the patient not to undergo attempted resuscitation

• patient’s death expected owing to terminal illness

• submersion of adults for > 1 hour

• efforts would be futile, as defined by the combination of all three of the following being present –

  • > 15 minutes since the onset of collapse

  • no bystander CPR prior to arrival of the ambulance

  • asystole (flat line) for > 30 seconds on the electrocardiogram (ECG) monitor screen (exceptions: drowning and drug overdose/poisoning).

Patients were also excluded from the trial if an immediate family member, relative or close friend who was present at the scene of the cardiac arrest indicated to the participating paramedic at the start of the resuscitation attempt that the person had previously expressed an opinion that they would not wish to take part in the AIRWAYS-2 trial. In practice, no patients were excluded for this reason.

Changes to trial eligibility criteria after commencement of the trial

In January 2015, the paramedic exclusion criteria were refined to define routine attendance at OHCA as attending at least two OHCA patients per year in whom resuscitation was attempted. The patient inclusion criterion regarding enrolment by the second trial paramedic on scene (where the first paramedic was not participating in the trial) was refined to state that the second paramedic could enrol the patient unless an AAM intervention had already occurred. Two additional patient exclusion criteria were added: ‘advanced airway device already in place when AIRWAYS-2 paramedic arrives at patient’s side (when the first paramedic to arrive is not participating in the AIRWAYS-2 trial)’ and ‘known to already be enrolled in another pre-hospital randomised trial’.

In April 2015, the paramedic inclusion criteria were updated to state that paramedics soon to be employed by a participating ambulance trust could participate, and that paramedics must be qualified to practise TI in their current clinical role. The patient inclusion criterion ‘must be in non-traumatic cardiac arrest outside hospital’ was changed to ‘patient has had a non-traumatic cardiac arrest outside hospital’, and the patient inclusion criterion ‘resuscitation is attempted or continued by emergency medical services (EMS) staff’ was changed to ‘resuscitation was commenced or continued by ambulance staff or responder’. The patient exclusion criterion ‘advanced airway device already in place when AIRWAYS-2 paramedic arrives at patient’s side (when the first paramedic to arrive is not participating in the AIRWAYS-2 trial)’ was changed to ‘advanced airway device inserted by another HCPC-registered paramedic already in place when AIRWAYS-2 paramedic arrives at patient’s side (when the first paramedic to arrive is not participating in the AIRWAYS-2 trial)’ and the patient exclusion criterion ‘estimated weight < 50 kg’ was removed.

In August 2015, the patient exclusion criterion ‘advanced airway device inserted by another HCPC-registered paramedic already in place when AIRWAYS-2 paramedic arrives at patient’s side (when the first paramedic to arrive is not participating in the AIRWAYS-2 trial)’ was changed to ‘advanced airway device inserted by another HCPC-registered paramedic, doctor or nurse already in place when AIRWAYS-2 paramedic arrives at patient’s side (when the first paramedic to arrive is not participating in the AIRWAYS-2 trial)’. The reason for this minor amendment was to update the protocol so that it reflected clinical practice (i.e. a trial paramedic would not remove an airway device that had already been inserted by a nurse or doctor).

Tracheal intubation (control group)

Tracheal intubation, the placement of a cuffed tube in the patient’s trachea to provide oxygen to the lungs and remove carbon dioxide (CO₂), has been generally recognised as the ‘gold standard’ of airway management. TI is used universally in comatose survivors of cardiac arrest following their admission to hospital.

i-gel (intervention group)

The intervention was insertion of the i-gel, a second-generation SGA, as an alternative to TI. Because of its speed and ease of insertion, this device is being increasingly used as the SGA of choice during OHCA in England. 29,30

Aspects of airway management common to both groups

A common approach to airway management, from basic to advanced techniques, was agreed by the participating ambulance services. This included the use of bag–mask ventilation (BMV) and simple airway adjuncts prior to AAM.

A standardised airway management algorithm1 (Figure 2) was developed by the four participating ambulance services to guide further actions should the initial approach to airway management prove unsuccessful.

FIGURE 2.

The AIRWAYS-2 trial treatment trial algorithm. (a) i-gel group: AIRWAYS-2 paramedic and at least one other person trained in CPR; (b) i-gel solo: single AIRWAYS-2 paramedic response; (c) intubation group: AIRWAYS-2 paramedic and at least one other person trained in CPR; and (d) intubation solo: single AIRWAYS-2 paramedic response. NP, nasopharyngeal; NPA, nasopharyngeal airway; OP, oropharyngeal; OPA, oropharyngeal airway. This figure is reproduced with permission from Taylor et al. 1 This is an Open Access article distributed in accordance with the terms of the Creative Commons Attribution (CC BY 4.0) license, which permits others to copy and distribute this work, for non-commercial use, with no derivatives, provided the original work is properly cited. See: https://creativecommons.org/licenses/by/4.0/. The figure includes minor additions and formatting changes to the original figure.

This figure is reproduced with permission from Taylor et al. 1 This is an Open Access article distributed in accordance with the terms of the Creative Commons Attribution (CC BY 4.0) license, which permits others to copy and distribute this work, for non-commercial use, with no derivatives, provided the original work is properly cited. See: https://creativecommons.org/licenses/by/4.0/. The figure includes minor additions and formatting changes to the original figure.

Care proceeded as normal for OHCA patients enrolled in the trial, aside from the initial AAM. All other interventions proceeded in accordance the standard resuscitation guidelines,24 which are disseminated widely in the UK and internationally. Patients who died at the scene were managed in accordance with nationally disseminated protocols. 28 Patients who did not die at scene were transported to hospital and treated using standard post-OHCA care pathways.

Owing to the emergency nature of the trial, we expected deviations from the AIRWAYS-2 trial treatment algorithm (see Figure 2). Protocol deviations could arise because paramedics have both strategies available to them. Usual practice follows a ‘step-wise’ approach from simple to more advanced techniques, but paramedics had clinical discretion to adapt airway management during OHCA to the patient’s anatomy, position and perceived needs. The trial protocol specified two attempts using the allocated strategy before proceeding to the alternative, but paramedics had discretion to deviate from the protocol on clinical grounds. Allowing discretion was necessary to avoid a paramedic feeling obliged to undertake an intervention that they believed to be against the patient’s best interests. This was also necessary to gain REC approval and professional support. 27

True crossover was defined as the patient receiving the incorrect intervention on the first airway management attempt; other deviations could occur during subsequent airway attempts. To try to reduce deviations as much as possible, monthly monitoring was carried out; research paramedics were required to follow up protocol deviations with the relevant AIRWAYS-2 paramedic and reiterate the correct procedures. We estimated that ≥ 80% adherence to the AIRWAYS-2 trial protocol was necessary to maintain the integrity of the trial, with < 10% true crossover. 1

Primary outcome

The primary outcome was mRS score measured at hospital discharge (or 30 days post OHCA if the patient was still in hospital). The mRS is a 7-point scale (0 to 6) widely used in OHCA research. 31,32 Scores are usually dichotomised as good outcome (0–3) or poor outcome/death (4–6; 6 indicates death). The full scale is:

• 0 – no symptoms at all

• 1 – no significant disability despite symptoms; able to carry out all usual duties and activities

• 2 – slight disability; unable to carry out all previous activities, but able to look after own affairs without assistance

• 3 – moderate disability; requiring some help, but able to walk without assistance

• 4 – moderately severe disability; unable to walk and attend to bodily needs without assistance

• 5 – severe disability; bedridden, incontinent and requiring constant nursing care and attention

• 6 – dead.

Patients were conveyed to and followed up in hospital, where mRS scores were collected by assessors blinded to treatment allocation. mRS score was determined by a research nurse, who assessed the patient using a simple flow chart that has been used previously to assess cardiac arrest survivors. 33

With the permission of the Health Research Authority CAG, we were able to collect survival data and mRS score at hospital discharge or 30 days after OHCA for all enrolled patients, regardless of their consent status, thereby ensuring close to 100% ascertainment of the primary outcome.

Secondary outcomes

The trial sought consent from survivors to collect additional data at hospital discharge, 3 months post OHCA and 6 months post OHCA (depending on consent option chosen). The three consent options were:

1. Active follow-up – data were collected from the patient’s medical records and they were invited to complete questionnaires about their ongoing health and well-being at 3 and 6 months post OHCA.

2. Passive follow-up – data were collected from the patient’s medical records, but they were not contacted again or invited to complete follow-up questionnaires.

3. No further involvement – no further information was collected, but it was clearly stated that the information already collected would be retained and included in the data analysis. Anonymity of the participant was assured.

A proportion of participants who experience an OHCA remain incapacitated; therefore, the trial was designed so that a personal consultee (usually a close relative) could provide an opinion on the follow-up option that would probably be preferred by the patient. 26

The following secondary outcomes were collected for all eligible patients, with all but the last two reported by participating paramedics:

• initial ventilation success, defined as visible chest rise

• regurgitation (stomach contents visible in the mouth or nose) and aspiration (stomach contents visible below the vocal cords or inside a correctly placed tracheal tube or airway channel of a SGA)

• loss of a previously established airway (patients with AAM only)

• sequence of airway interventions delivered (patients with AAM only)

• ROSC

• airway management in place when ROSC was achieved, or resuscitation was discontinued

• chest compression fraction (in a subset of patients in two ambulance services)

• time to death.

For patients who survived to admission to hospital (estimated to be ≈ 20% of enrolled patients before the trial started), length of intensive care stay and length of hospital stay were also collected. For patients who survived to hospital discharge (estimated to be ≈ 9% of enrolled patients before the trial started), QoL using the EuroQol-5 Dimensions, five-level version (EQ-5D-5L), was collected at the time of discharge. For patients who survived beyond hospital discharge, date of death was collected (if applicable), mRS score was collected at 3 and 6 months post OHCA, and QoL (using the EQ-5D-5L) was collected at 3 and 6 months post OHCA.

Chest compression fraction was measured in a subset of patients. Good-quality, continuous CPR is associated with increased survival and improved neurological outcomes following cardiac arrest,19,34 and compression fraction is the standardised way of measuring and expressing this. 35 In this trial, standard resuscitation protocols were agreed with all participating ambulance services. These specified that patients receive continuous chest compressions as soon as an advanced airway device (i-gel or tracheal tube) was placed successfully. Therefore, patients in both groups should receive continuous chest compressions.

The compression fraction is defined as the proportion (or percentage) of resuscitation time without spontaneous circulation during which chest compressions are administered; the higher the compression fraction, the better the quality of CPR and the more likely it is that the patient will survive. 36 Comparison of the compression fraction between the two groups could help to explain the trial findings. Measuring and reporting compression fraction allows heterogeneity between trials to be more consistently described. A suggested mechanism by which SGAs may improve the outcomes of OHCA is a reduction in interruptions to CPR (with an accompanying increase in compression fraction).

Compression fraction is not routinely measured during OHCA in England but it is technically possible. 37 Measurement of compression fraction requires the use of a modified defibrillator, but it was not practical or affordable to measure this in all enrolled patients. Instead, the trial implemented technology that enabled compression fraction to be routinely measured during CPR in a subset of enrolled patients and collected these data alongside the other outcome measures. The technology used was the CPR card (Laerdal Medical AS, Stavanger, Norway), a small disposable device placed in the centre of the patient’s chest during CPR. The specific device we used gives no feedback to the user but records data that can be retrieved subsequently.

Resource use data to be used for the trial cost-effectiveness analysis and longer-term function were also collected (see Economic evaluation).

Adverse events

Serious adverse events (SAEs) and other adverse events (AEs) were recorded and reported in accordance with the Good Clinical Practice guidelines38 and the sponsor (South Western Ambulance Service NHS Foundation Trust)’s Research Related Adverse Event Reporting Policy.

Data on AEs were collected from the start of the intervention for the duration of the participant’s post-operative hospital stay and for the 6-month follow-up period if the patient consented to ongoing data collection. Any elective surgery/intervention/treatment (e.g. planned non-cardiac surgery) during the follow-up period that was planned prior to enrolment to the trial was not reported as an unexpected SAE.

Changes to trial outcomes after commencement of the trial

In April 2015, the primary outcome measure was amended to state that mRS score could be measured either at hospital discharge or 30 days post OHCA, instead of at hospital discharge only. The reason for this change was that some patients were proving to have very long hospital stays. Indeed, in some cases a patient could remain an inpatient for years, meaning that they would never record a primary outcome measure. It was noted that for patients who survived to hospital discharge (or were still inpatients 30 days after their OHCA) the mRS score would be determined by a research nurse who would assess the patient using a simple flow chart that has been used previously to assess patients who have had a cardiac arrest. 33 Any patient who did not survive to discharge would automatically be assigned a score of 6 (dead).

Paramedic sample size

In our feasibility trial the mean number of patients enrolled per participating paramedic was 3.6 per year. Therefore, to enrol the 9070 patients within the 2-year period of the trial, we estimated that we would need to recruit at least 1300 paramedics. Across the four ambulance services participating in the AIRWAYS-2 trial, there were > 4300 eligible paramedics; therefore, we needed to enrol > 30% of these paramedics.

Identification of patients with out-of-hospital cardiac arrest

All eligible patients attended by a participating paramedic were automatically enrolled in the trial under a waiver of consent. Therefore, it was essential to establish mechanisms that would reliably identify every one of these patients. We achieved this by identifying every OHCA (where resuscitation was attempted) that occurred in the participating ambulance services throughout the trial period, along with the subset of patients eligible for trial inclusion. The process to achieve this is described in the following paragraph. It allowed regular review by the DMSC and supported a complete ITT analysis (see Statistical methods, Sensitivity analyses of the longer-term secondary outcomes).

In April 2011, the Department of Health and Social Care introduced survival from cardiac arrest as part of the Ambulance Service National Quality Indicator set. 40 ROSC and survival to hospital discharge rates are reported for all patients who have resuscitation started or continued by a NHS ambulance service after an OHCA. 41 For this reason, all cardiac arrests are routinely identified by ambulance services in England, with regular data collection and return. This process was being strengthened through the introduction of an electronic patient record and a national OHCA registry, based at the University of Warwick. 42 To ensure near-complete patient identification, we used a triangulation method developed during the feasibility trial. 25 Data were collected on all OHCAs occurring within an ambulance service from three separate sources:

1. Direct paramedic report – participating paramedics were asked to complete a CRF immediately after each eligible OHCA that they attended, and to notify the co-ordinating research paramedic by telephone, text or e-mail.

2. Daily review of the ambulance computer-aided dispatch (CAD) system by a project research paramedic to identify all 999 calls from the previous 24 hours identified as suspected or confirmed cardiac arrest, and follow up with the relevant ambulance staff to determine whether or not OHCA had occurred.

3. Regular review of the OHCA data routinely collected by that ambulance trust and reported as part of the Ambulance Service National Quality Indicator set. 40 This is usually based on the clinical record (paper or electronic) routinely completed by ambulance staff after each case that they attend.

Source 1 was the primary data source for the AIRWAYS-2 trial. However, by triangulating data from all three sources it was possible to reliably identify all, or nearly all, OHCAs where resuscitation was attempted during the trial. Although it was possible for an eligible OHCA to be overlooked by this triangulation process, it would require that a cardiac arrest not be reported to the research team by a participating paramedic, not be identified as an OHCA on the CAD and not be picked up by the ambulance trust’s routine identification and reporting system. We estimated that the chance of this happening was very low, thereby ensuring an exceptionally high rate of eligible patient identification that reduced any bias to an absolute minimum.

Out-of-hospital treatment phase (data collection by paramedics)

After treating an eligible OHCA patient, the participating paramedic responsible for airway management completed a CRF to capture baseline and secondary outcome data. The CRF was completed at the same time as routine ambulance service paperwork: immediately after the patient had been handed over to the receiving hospital team or resuscitation attempts had been discontinued at the scene. The CRF was then returned as soon as possible (preferably within 24 hours) to the co-ordinating research paramedic by a secure method chosen by each ambulance trust (e.g. post, secure fax or e-mail). Occasionally, the participating paramedic would not complete the form immediately, in which case they were contacted by the research paramedic subsequently and encouraged and supported to do so.

Even when this did not occur, relevant data could be extracted from the routine ambulance service record within 48 hours, allowing the patient to be followed up to seek consent and collect primary and secondary outcome data. Ambulance services reliably collect data regarding the individuals attending each patient and the time of staff arrival; therefore, for every eligible patient, the attending ambulance paramedic(s), trial allocation and a range of baseline data could be determined with near-100% accuracy.

Hospital discharge (data collected by hospital staff)

Once a patient had been admitted to hospital, the consent and follow-up process was co-ordinated by a research nurse allocated to each participating ambulance service. This was identified as a separate, hospital-based post to ensure that consent and follow-up was blinded to treatment. The research nurse was usually based in the main ‘heart attack centre’ or major receiving hospital for that region. 43

Each research nurse received regular lists of enrolled patients who had been brought to the receiving hospitals in that ambulance service region. The research nurse co-ordinated the process of identification, consent and follow-up data collection with support from the central team. Although the research nurse undertook this personally where necessary, in most cases the consent and follow-up processes were undertaken by existing research staff at the receiving hospitals.

Data presentation

Continuous variables were summarised using the mean and standard deviation (SD), or the median and interquartile range (IQR) if the distribution was skewed. Categorical variables were summarised as number and percentage.

Adjustment in models

The intention was to adjust all models for paramedic as a random effect and for the three stratification factors included in the randomisation as fixed effects [NHS ambulance trust (YAS, SWAST, EMAS and EEAST), paramedic experience (≥ 5 years and < 5 years) and distance from paramedic’s base ambulance station to the nearest hospital (≥ 5 miles and < 5 miles)]. Where it was not possible to fit paramedic as a random effect, the clustering within paramedic was accounted for using a clustered sandwich estimator, or clustered bootstrap where this was not possible.

Primary and secondary pre-hospital discharge outcome models

The primary outcome of mRS score at discharge or 30 days post OHCA [presented dichotomously as good functional recovery (0–3) or poor functional recovery/death (4–6; 6 indicates death)], and other binary outcomes were analysed using a multilevel logistic regression model. Repeated mRS scores were analysed using multilevel logistic regression at the separate time points owing to convergence issues. The treatment effects for these models were presented as odds ratios (ORs) and 95% confidence intervals (CIs). Compression fraction was transformed owing to skewness and the log of 100 minus the compression fraction was fitted using a multilevel Gaussian model, with the treatment effect presented as a geometric mean ratio (GMR) and 95% CI.

The following secondary outcomes were described but not formally compared: sequence of airway interventions delivered, airway management in place when ROSC was achieved or resuscitation was discontinued, and length of ICU stay. Time to death or last follow-up was formally compared in place of length of ICU and hospital stays. For time to death (up to 72 hours), patients who were known to be alive longer than 72 hours post OHCA were censored at 72 hours (i.e. given a time to death of 72 hours). For time to death or last follow-up, survivors who did not consent to active or passive follow-up were censored at ICU discharge, survivors who consented and provided 6 months’ follow-up data were censored at 6 months post OHCA, survivors who consented and provided 3 months’ but not 6 months’ follow-up data were censored at 3 months post OHCA, and survivors who consented and provided 30 days’/hospital discharge data but not 3 months’ or 6 months’ follow-up data were censored at hospital discharge.

Both time to death or last follow-up and time to death (up to 72 hours) were analysed using Cox proportional hazards models stratified by NHS ambulance trust to allow for varying baseline hazards and adjusted for paramedic experience and distance from base ambulance station. These models were adjusted for clustering of paramedic using a clustered sandwich estimator and presented as hazard ratios (HRs) and 95% CIs.

Sensitivity analyses of the primary outcome

Three pre-specified exploratory sensitivity analyses were performed for the primary outcome. The first extended the trial population to include patients attended by a participating paramedic but who were not resuscitated (i.e. trial patients plus non-resuscitated patients). This was prompted by feedback from a pre-planned, closed interim analysis of half the sample considered by the DMSC. 27 The second and third sensitivity analyses, restricted to the cohort of patients who received AAM (as allocated and treatment received comparisons), were planned from the outset. All three sensitivity analyses were analysed using multilevel logistic regression.

Additional analyses of the primary outcome

In the sensitivity analysis of the primary outcome restricted to the cohort who received AAM, patients who did not receive either trial treatment were excluded. Owing to concerns that this analysis could be prone to bias, one additional analysis was performed to assess the causal effect of the treatment received on the primary outcome. This analysis used two-stage least squares with two instruments: randomisation and an indicator of whether one or two paramedics initially attended the OHCA. In the first stage, the treatment received was regressed on the two instruments and the interaction between the two instruments. Predicted probabilities were obtained from the first-stage model. In the second stage, the mRS score was regressed on these predicted probabilities and the stratification factors used in randomisation. For more information relating to the model fitted, see Appendix 4.

Subgroup analyses of the primary outcome

Two subgroup analyses were planned: (1) Utstein comparator group (OHCA with a likely cardiac cause that was witnessed and had an initial rhythm amenable to defibrillation,46 estimated to make up ≈ 20% of the total) versus non-comparator group and (2) OHCA witnessed by paramedic (estimated to make up 6% of the total) or not. These two subgroup analyses were analysed on an ITT basis.

Because of concerns about ventilation success raised during the trial, an additional subgroup analysis of the primary outcome comparing patients whose i-gel or intubation airway management attempt(s) were or were not ‘successful’ during the first and/or second attempt was also performed. This analysis was performed on an as-treated basis (i.e. according to the first AAM the patient had received). In addition, this third unplanned subgroup analysis included patients who had received at least one AAM using an i-gel and/or TI only.

The treatment effects in subgroups were compared by testing for an interaction between paramedic allocation and the subgroup variable. We described the outcomes in the subgroups and tested for differences in the primary outcome between subgroups by including interaction terms in the models, although we recognised that the power to detect such differences was low as the proportions in the subgroups were unequal.

Longer-term secondary outcomes

The longer-term secondary outcomes were mRS score measured at 3 months and 6 months and QoL [single summary index and visual analogue scale (VAS)] measured at 30 days/hospital discharge, 3 months and 6 months. These longer-term outcomes were obtained from patients who had survived to the follow-up time points and had provided active consent.

The five dimensions of the EuroQol-5 Dimensions (EQ-5D) – mobility, self-care, usual activities, pain/discomfort and anxiety/depression – were described for actively consented survivors. These five dimensions were transformed into a single summary index score using a method that mapped these scores onto the EuroQol-5 Dimensions, three-level version (EQ-5D-3L), value set. 47 A value of 0 was assigned for both VAS and single summary index for patients who had died.

Only patients with outcome data were included in the main analyses of these outcomes (complete-case analysis). The dichotomised mRS scores were analysed using multilevel logistic regression with paramedic fitted as a random effect. Both the single summary index and VAS scores had large spikes at 0 due to the large number of deaths, which meant that a normal or log-normal regression model was inappropriate. Consequently, these two QoL outcomes were analysed using a two-part beta-binomial model. For the purposes of modelling, the QoL scores of survivors were transformed as follows:

where y is the QoL score, a is the lowest possible score (single summary index –0.59, VAS 0), b is the highest possible score (index 1, VAS 100), N is the total number of survivors with data and yⁿ is the transformed score. 48 This transformation was necessary for the purposes of beta regression as it guaranteed that the transformed scores were between 0 and 1 (excluding 0 and 1).

Two estimates were produced from the two-part beta-binomial model. The first, which is the binomial part, is the OR for survival (‘alive vs. dead’). The second estimate, which is the beta part, relates to the QoL of survivors (‘score for survivors’). Thus, these models were able to assess whether or not the use of the i-gel reduces the risk of death and, if the patient survives, assess whether or not it improves the patient’s QoL. An estimate > 1 for ‘alive vs. dead’ means that the odds of survival in the i-gel group is higher than in the TI group. Similarly, an estimate > 1 for ‘score for survivors’ means a better QoL in the i-gel group than in the TI group.

All longer-term outcomes were fitted to each time point separately because convergence issues prevented the fitting of longitudinal models. Convergence issues were also encountered when including paramedic as a random effect in the QoL models. Thus, the CIs were estimated using clustered bootstrapping. 49,50 A total of 1000 cluster bootstrap samples were created by sampling the paramedic clusters with replacement to obtain 1375 paramedic clusters in each bootstrap sample. The ‘alive vs. dead’ and ‘score for survivors’ estimates were obtained from each of the 1000 cluster bootstrap samples by applying the two-part beta-binomial model. The SD of each set of estimates (SD_bootstrap) was then used as an approximation of the standard error (SE) and the 95% CIs were estimated using the formula:

Both the clustered bootstrap and two-part beta-binomial models were performed in SAS^® version 9.4 (SAS Institute Inc., Cary, NC, USA; SAS and all other SAS Institute Inc. product or service names are registered trademarks or trademarks of SAS Institute Inc. in the USA and other countries. ^® indicates USA registration) and all other analyses were performed in Stata.

Sensitivity analyses of the longer-term secondary outcomes

Two sensitivity analyses were performed on the longer-term secondary outcomes to examine the effect of missing data. The first was the ‘worst-case scenario’, in which the worst possible score for a survivor was assigned to known survivors with missing data. In this scenario, patients whose survival status was unknown were assumed to have died. The ‘imputed case scenario’ was the second sensitivity analysis. In this scenario, multiple imputation (60 imputations) was performed using the ice command in Stata. Estimates were combined using Rubin’s rules.

In the worst-case scenario, multilevel logistic regression was performed for the mRS score at 3 months and 6 months post OHCA. The two-part beta-binomial model was used to analyse the QoL outcomes at 30 days/hospital discharge, 3 months and 6 months post OHCA. For the QoL outcomes, the 95% CIs were adjusted using the clustered bootstrap method described in Longer-term secondary outcomes.

In the ‘multiple imputed case scenario’, the variables included in the multiple imputation model were age; sex; length of ICU stay; treatment group; the randomisation stratification variables; and QoL and mRS scores at 30 days/hospital discharge (whichever was earlier), 3 months and 6 months post OHCA. Predictive mean matching was used for continuous variables. The percentages of missing data were calculated for patients who survived to 30 days/hospital discharge (whichever was earlier) for all QoL and mRS score outcomes and time points in turn. The number of imputations (which was 60) was based on the maximum missingness percentage. For mRS score at 3 months and 6 months post OHCA, multilevel logistic regression with paramedic as a random effect was performed on the multiple imputed data sets and the estimates were pooled using Rubin’s rules. In this scenario, the QoL secondary outcomes were analysed using the two-part beta-binomial model. To obtain the cluster bootstrap-adjusted 95% CIs, the clustered bootstrap was performed to produce the 1000 bootstraps samples. This was followed by multiple imputation (60 imputations) on each of the bootstrap samples as recommended by Schomaker and Heumann. 51 Rubin’s rules were then used to combine the treatment estimates in each of the 1000 bootstrap samples and, as described in Longer-term secondary outcomes, the SDs of these two sets of treatment estimates were used as proxies for the SEs in the calculation of the CIs. These analyses were completed using Stata for the multiple imputation and SAS for the clustered bootstrap and model fitting.

Frequency of analyses

The original intention was for the primary analysis to take place when follow-up was complete for all enrolled participants. Formal interim analysis was planned at the mid-point of patient enrolment (after 12 months) and was presented to the DMSC. Safety data were reported together with any additional analyses the committee requested. In these reports the data were presented by group, but the allocation remained masked.

During the sixth DMSC meeting in September 2017, the DMSC recommended that the primary outcome be analysed prior to completion of patient follow-up and published first. There were three main reasons for early reporting: (1) to realise patient benefit as soon as possible, (2) to inform policy and guidance at a time of increased interest in the future of TI52 and (3) to co-ordinate with publication of the PART, a comparable trial undertaken in North America. 53 The DMSC was happy for this to take place if all relevant data fields could be locked down. This proposal was discussed with and agreed by the National Institute for Health and Care Research (NIHR) Health Technology Assessment (HTA) programme and the Trial Steering Committee (TSC) at their fourth meeting in October 2017.

Economic evaluation aims and objectives

The economic evaluation aimed to estimate the incremental cost-effectiveness of the i-gel compared with TI in non-traumatic OHCA adults in line with the AIRWAYS-2 trial.

Economic evaluation overview

The perspective of the evaluation was that of the NHS and Personal Social Services (PSS), as recommended by the National Institute for Health and Care Excellence (NICE). 54 The perspective for outcomes was that of the patients undergoing treatment. The primary outcome measure for the cost-effectiveness analysis was quality-adjusted life-year (QALYs), estimated using the EQ-5D-5L. 55,56 Good practice guidelines on the conduct of economic evaluations were followed. 54,57,58 Table 2 summarises the key aspects of the economic evaluation methods.

Form of analysis, primary outcome and cost-effectiveness decision rules

A cost-effectiveness analysis (specifically a cost–utility analysis) using QALYs as the primary outcome measure was conducted, as advocated by NICE. 54 QALYs combine both quantity of life and QoL into a single measure. Incremental costs (the difference in mean costs between the i-gel and TI groups) were divided by incremental QALYs (the difference in mean QALYs between the groups) and presented as the incremental cost-effectiveness ratio (ICER), which quantifies the incremental cost per QALY gained by switching from using TI to i-gel. The economic evaluation analyses were performed on an ITT basis.

The i-gel was considered cost-effective if the ICER fell below £20,000, which is generally considered to be the threshold that NICE adopts for considering an intervention to be cost-effective. 59

Time horizon

A within-trial analysis, taking a 6-month time horizon, was conducted. It was anticipated that all major resource use would occur within this time frame and, therefore, be captured. Our time horizon began when the first paramedic arrived at the OHCA scene and continued until 6 months later.

Data set

The base-case analysis included all trial patients (see Economic evaluation overview), except seven patients who were transported to hospital but could not be identified and were lost to further follow-up (three randomised to TI and four randomised to i-gel). It was felt that there was insufficient information on these patients to reasonably impute their follow-up data.

Collection of resource use and costs

Resource use data were collected on all significant health service resource inputs for the trial patients to the end of the 6-month follow-up period. Detailed resource use data on the pre-hospital phase in the patient care pathway were collected on the trial CRFs, and inpatient data were largely obtained from HES data sets. CRFs for the pre-hospital phase were completed by the paramedics attending the OHCA patients and by the research paramedics using data from the ambulance CAD system. A small amount of inpatient resource use was captured on the in-hospital CRFs, and primary and community care resource use post hospital discharge was captured on the follow-up questionnaires at 3 and 6 months post OHCA for patients who consented to follow-up. The main resource use categories costed are listed in Table 3, along with details of the sources of unit cost information for each resource category.

Availability of resource use and cost data

Given the large numbers of patients and hospitals involved in the AIRWAYS-2 trial, the trial CRFs asked limited numbers of questions on health-care resource use. The intention was to make use of routinely held data and collect the majority of secondary care resource use from HES. Because we had several issues obtaining data from four HES data sets (ED, inpatients, critical care and outpatients), we made contingency plans early in the trial to mitigate the risk of not receiving all the HES data we would need for the trial cost-effectiveness analysis.

At the outset of the trial, some additional resource use data items were added to the trial data collection forms. Detailed information on trial CRFs captured the date and time of movements between different levels of care during the inpatient admission. An additional question was also added to the 3- and 6-month follow-up questionnaires asking about overnight hospital stays. However, without HES data we would have no information on interventions and procedures patients receive in hospital (notably CT and percutaneous coronary interventions) nor any information after hospital discharge about further contact with secondary care (re-admissions, outpatient appointments, subsequent ED visits) beyond the information described above on the number of additional nights in hospital captured on the follow-up questionnaires.

To further mitigate against a possible lack of HES data as the trial neared completion, we asked the top five hospitals (i.e. the five hospital trusts that had received the most patients) in each of the four ambulance trust regions enrolling patients to the trial for some additional data for up to 50 AIRWAYS-2 patients taken to their hospital. For the index admission, this additional retrospective CRF captured the number of CT and magnetic resonance imaging scans, angiograms performed (and whether or not these included a percutaneous coronary intervention) and any other surgery. For the period from hospital discharge to 6 months post OHCA, the trial CRFs captured information on hospital re-admissions (length of stay and number of days in intensive care) and any other surgery. We sought information on a random sample of 50 patients taken to each hospital (or all patients taken there if this was < 50), sampled in the following ratio: one-third died in the ED, two-thirds admitted to hospital. This extra data collection was made possible by support from the NIHR critical care clinical specialty leads and research nurses.

The intention was for these secondary care resource use data, captured for a sample of AIRWAYS-2 patients on trial CRFs, to be summarised and costed. The mean resource use and associated costs would then be calculated for three subgroups of patients:

1. patients who died in ED

2. patients who survived to hospital admission but died in hospital

3. patients who survived to hospital discharge.

The mean costs of procedures and scans in hospital, and re-admissions, calculated for these subgroups would then be applied to all AIRWAYS-2 patients who were brought to hospital. However, these data were not used, because HES data were obtained and used in our primary analysis. However, having collected these additional data, an extension to this work will compare this resource use and associated costs with the HES data.

Although there was very good case ascertainment for three of the HES data sets received, there were considerably fewer patients in the critical care data set than expected. Based on CRF data, 1450 patients were admitted to intensive care following their OHCA; however, the HES critical care data set contained records for only 314 patients. Given this wide disparity between data sources, we did not use the HES critical care data set; time in intensive care was taken from the CRFs instead. NHS Digital has kindly investigated this issue. The original request for each identified patient was for data from the date of OHCA to 6 months post OHCA. It appears there may be an issue with dates: from a preliminary check, HES critical care records relating to ≈ 1250 patients were identified when data from date of OHCA minus 7 days through to 6 months were extracted, much more in line with expectations. However, it is still unclear why this issue exists. There was a considerable amount of data cleaning required for the resource use figures. For further details, see Appendix 5.

Attaching unit costs to resource use

Unit costs for hospital and community health-care resource use were largely obtained from national sources, for example NHS Reference Costs for ward costs, scans and surgery,62 and Unit Costs of Health and Social Care for community costs. 64,65 Resources were valued in 2017/18 Great British pounds, and any unit costs not in 2017/18 prices have been adjusted to 2017/18 prices using the NHS Cost Inflation Index (NHSCII). 66 For a summary of the sources of unit cost information, see Table 3. For further details on all unit costs and their sources, see Appendix 6.

Measurement of health-related quality of life and quality-adjusted life-years

Missing data

Recommended techniques for handling missing data were used. 71 We first summarised the number of missing data for resource use and outcomes (EQ-5D scores) descriptively. Exploratory analyses were conducted to explore the possible mechanisms and patterns of missing data. 72 Logistic regressions were used to explore associations between missingness and baseline variables, and missingness and previously observed outcomes. If the number of missing data was small (< 1% of cases), then unconditional or conditional mean imputation would be sufficient. However, we anticipated that it would be necessary to use multiple imputation to impute missing values. Multiple imputation is a flexible approach that is valid if data are assumed to be missing at random (the probability that data are missing does not depend on the unobserved values, conditional on the observed data). 72 This assumption was assessed.

Multiple imputation uses regression to predict m values for each missing data cell, and it enables all key variables used in the economic evaluation and demographic data (both complete and incomplete) to be used to predict the values of missing data cells. In accordance with guidelines,72,73 multiple imputation using chained equations was conducted, and the number of imputations set to be at least equal to the percentage of incomplete cases. 73 Multiple imputation was performed separately for each treatment group. Although the data are multilevel in nature (patients at level 1 enrolled by paramedics at level 2), it was not possible to perform multiple multilevel imputation, since the number of patients per cluster (paramedic) was too small. 74–76

Multiple imputation can be conducted, for example, at an aggregated level of total costs, or at a disaggregated level of individual resource use items or EQ-5D domains. Given that imputing large numbers of variables may make the model difficult to estimate, a balance between the two is likely to be required. The patterns of missing data for resource use/costs and outcomes were used to determine the approach to multiple imputation. For example, data collected using a patient follow-up questionnaire may have similar patterns of missing data, in which case the total costs for that follow-up can be imputed, rather than individual resource use items. For each variable with missing data, individual regressions were specified and tailored to the type of data being predicted. Linear regression with prediction mean matching was used because it is particularly flexible.

Once multiple imputation had been conducted, tabulations and summaries of the observed and imputed data were compared to check the validity of the imputations. Rubin’s rule was then used to summarise data across the m data sets. 77 This approach accounts for the variability both within and between imputed data sets and takes uncertainty in the estimated mean into account.

Within-trial statistical analysis of cost-effectiveness results

Analyses were conducted in Stata and Microsoft Excel^® 2016 (Microsoft Corporation, Redmond, WA, USA).

Initially, descriptive summaries of resource use, costs and HRQoL were performed using means, SDs and SEs around the means using both the central limit theorem and bootstrapping. Cost data are typically positively skewed, but, regardless of this, costs were summarised using the arithmetic mean, because it is this, combined with the total number of patients, that relates to the total budget impact of an intervention.

Given that the AIRWAYS-2 trial is a cluster randomised trial, statistical methods for combining costs and outcomes needed to take account of the correlation between costs and outcomes at both the individual and the cluster level. 78 We used multilevel liner regression modelling to take account of the clusters, since this flexible framework can also accommodate missing data and cost skewness. 79

The ICER was derived from the average costs and QALYs gained in each treatment group, producing an incremental cost per QALY gained of the i-gel compared with TI. Non-parametric bootstrapping of costs and QALYs was used to quantify the degree of uncertainty around the ICER. Results are expressed in terms of a cost-effectiveness acceptability curve (CEAC), which indicates the likelihood that the i-gel is cost-effective for different levels of willingness to pay for health gain. Although the i-gel is considered cost-effective if the ICER falls below £20,000, the ICERs and CEACs presented allow decision-makers to assess cost-effectiveness at a willingness-to-pay threshold of their choice.

The ICER is a ratio of incremental costs (the difference in mean costs between the i-gel and TI groups) divided by incremental QALYs. A negative ICER can be the result of positive incremental costs and negative incremental QALYs, or negative incremental costs and positive incremental QALYs, but has a different meaning depending on the direction of these differences. Uncertainty around the ICER becomes infinite if there is a small difference in QALYs and the denominator of the ICER encompasses zero. If either of these scenarios arise, it is helpful to rearrange the cost-effectiveness decision rule to consider incremental net monetary benefit (NMB) instead, and make comparisons without using ratios.

For a given willingness-to-pay threshold for an additional QALY, incremental NMB is the value of incremental effects on a monetary scale, incremental QALYs multiplied by threshold, minus incremental costs. If incremental NMB is positive for any given threshold, then the i-gel is considered cost-effective compared with TI at that threshold. Because NMB tends to be normally distributed, we can calculate a 95% CI around it; this will be done using the non-parametric bootstrap replicates of costs and QALYs.

Discounting

Costs and effects were not discounted as our time horizon was < 12 months.

Sensitivity analysis

Univariate sensitivity analyses were used to investigate the impact on costs and cost-effectiveness results of variation in key parameters and major cost drivers, and to investigate the impact of uncertainty on the cost-effectiveness results.

Factors examined in the sensitivity analyses for costing were varying the unit costs for paramedics, ED attendance, intensive care stay and inpatient care. The impact of any high-cost patients was also investigated.

Factors examined in the sensitivity analyses for health outcomes were varying the assumed baseline QoL (assuming a baseline utility of 0 rather than –0.402) and considering life-years as an alternative outcome to QALYs.

For details of all sensitivity analyses, see Appendix 7.

Subgroup analysis

No subgroup analyses were pre-planned for the cost-effectiveness analyses.

Primary analysis

A similar proportion of patients in each treatment group had a favourable functional outcome (mRS score) at 30 days/hospital discharge (TI, 6.8%; i-gel, 6.4%).

The results of the logistic regression model showed that the odds of a favourable functional recovery were higher in the TI group than in the i-gel group [OR 0.92 (95% CI 0.77 to 1.09; p = 0.33), ADP experiencing a good outcome –0.6% (95% CI –1.6% to 0.4%; p = 0.24), RR 0.92 (95% CI 0.79 to 1.08; p = 0.32)]. Table 8 and Figure 6 contain the details of the primary outcome.

FIGURE 6.

Primary outcome analysis results. Reproduced with permission from JAMA 2018;320(8):779–91. 27 Copyright © 2018 American Medical Association. All rights reserved.

Reproduced with permission from JAMA. 2018. 320(8):779–91. 27 Copyright©2018 American Medical Association. All rights reserved

Figure 7 and Appendix 1, Figure 23, contain information about ROSC on arrival, AAM and ROSC during/after AAM, and the breakdown of mRS scores in each of these groups. The median time from OHCA to mRS assessment was slightly lower in the TI group (25 days) than in the i-gel group (28 days). Crossover was more common among patients randomised to TI than among those randomised to i-gel (see Table 6, Figure 7 and Appendix 1, Figure 23).

FIGURE 7.

Interventions received and patient outcome by trial allocation. a, A total of 72 patients in the TI group (2.1%) received a non-trial SGA (i.e. not the i-gel) only, all of whom had an mRS score of 4–6 (71 deaths). Among these 72 patients, two had ROSC on arrival. b, A total of 36 patients (0.9%) in the i-gel group received a non-trial SGA (i.e. not the i-gel) only, all of whom had an mRS score of 4–6 (35 deaths). Among these 36 patients, none had ROSC on arrival. Note: there were 41 patients (TI, n = 17; i-gel, n = 24) with missing ROSC on arrival of trial EMS clinician. Among these 41 patients, 39 (TI, n/N = 15/17; i-gel, n/N = 24/24) had an mRS score of 4–6 (37 deaths: TI, n/N = 14/15; i-gel, n/N = 23/24).

Sensitivity analyses

The first analysis was fitted on trial patients plus patients who were attended by a trial paramedic but not resuscitated, and this analysis was performed on an ITT basis. There were higher odds of a favourable functional recovery in the TI group than in the i-gel group [TI, 2.8%; i-gel, 2.7%; OR 0.96 (95% CI 0.81 to 1.14; p = 0.63), ADP –0.2% (95% CI –0.6% to 0.3%; p = 0.45), RR 0.96 (95% CI 0.81 to 1.13; p = 0.64)] (Figure 8; see also Appendix 1, Table 35).

FIGURE 8.

Sensitivity analyses of the primary outcome. a, Complete-case analysis of the primary outcome. Data missing for seven patients (TI, n = 3; i-gel, n = 4). b, Trial patients plus patients who were attended by a trial paramedic but not resuscitated. Data missing for seven patients (TI, n = 3; i-gel, n = 4). c, Trial patients who received at least one AAM attempt. Data missing for four patients (TI, n = 1; i-gel, n = 3). d, Trial patients who received at least one AAM attempt. Data missing for four patients (TI, n = 2; i-gel, n = 2).

The second sensitivity analysis consisted of analysing trial patients who received at least one AAM attempt on an ITT basis. There were no clear differences (not formally tested) in the baseline characteristics of patients in the trial population, the population that received AAM and the population that did not receive AAM (see Appendix 1, Table 33). A larger proportion of patients had a good functional recovery in the i-gel group (3.9%) than in the TI group (2.6%) [OR 1.57 (95% CI 1.18 to 2.07; p = 0.002), ADP 1.4% (95% CI 0.5% to 2.2%; p = 0.001), RR 1.54 (95% CI 1.18 to 2.01; p = 0.002)] (see Figure 8 and Appendix 1, Table 35).

For the third sensitivity analysis, trial patients who received at least one AAM attempt were compared according to the treatment they had received first. No clear differences (not formally tested) in the baseline characteristics between these two groups were observed (see Appendix 1, Table 34). A larger proportion of patients with a good functional recovery was observed in the i-gel-first group: 2.0% in the TI-first group and 4.2% in the i-gel-first group [OR 2.06 (95% CI 1.51 to 2.81; p < 0.001), ADP 2.1% (95% CI  1.2% to 2.9%; p < 0.001), RR 2.00 (95% CI 1.48 to 2.70; p < 0.001)] (see Figure 8 and Appendix 1, Table 35).

Additional analysis

There was a differential adherence proportion in the two randomised treatment groups: 61.9% of patients in the TI group received TI as their first AAM whereas 82.1% of patients in the i-gel group received i-gel as their first AAM. There were nine patients (TI, n = 6; i-gel, n = 3) in whom it was unknown whether or not any AAM had been performed, and there were 1707 patients (TI, n = 985; i-gel, n = 722) who received no AAM. A total of 7580 patients (TI, n = 3419; i-gel, n = 4161) had received an AAM, 108 (TI, n = 72; i-gel, n = 36) of whom received a non-trial SGA. There were seven patients (TI, n = 3; i-gel, n = 4) who could not be identified and, thus, were missing the primary outcome. Therefore, 9280 patients (TI, n = 4401; i-gel, n = 3879) were included in the instrumental variables analysis. Baseline characteristics were similar between the four groups (split by randomised group and further split by adherence) (see Appendix 1, Table 36).

A causal ADP of –0.49% (95% CI –5.38% to 4.40%; p = 0.84) was obtained from this analysis (Figure 9). This result showed that a strategy of TI first had a better chance of a good functional recovery than a strategy of i-gel first. The CI is wider than that obtained in the primary analysis and includes differences more than the pre-specified clinically important difference of 2% in both directions. See Figure 9 for an illustration of the differences in the results of the ITT, as-treated and causal analyses.

FIGURE 9.

Intention-to-treat, as-treated and causal analyses of the primary outcome. a, Data missing for seven patients (TI, n = 3; i-gel, n = 4). b, Data missing for four patients (TI, n = 2; i-gel, n = 2). c, Data missing for seven patients (TI, n = 3; i-gel, n = 4).

Subgroup analyses

The results of the two pre-specified subgroup analyses and one additional subgroup analysis explored at the request of the DMSC are presented in Figure 10. The first tested for any difference in the primary outcome between the two randomised groups for the Utstein comparator versus non-Utstein comparator groups. No significant interaction was found between these two subgroups (p = 0.07). The second subgroup analysis tested for any difference in the primary outcome between the OHCA witnessed by ambulance staff and OHCA not witnessed by ambulance staff groups. No significant interaction was found between these two subgroups (p = 0.37). The third analysis was performed on the as-treated groups and compared the subgroup of patients who had initial ventilation success with patients who had no initial ventilation success. A significant interaction between these two groups was found (p = 0.001).

FIGURE 10.

Subgroup analyses. Note that the Utstein comparator group includes patients with an OHCA with a likely cardiac cause that is witnessed and has an initial rhythm amenable to defibrillation. For the Utstein comparator vs. non-Utstein comparator analyses, there were missing data for 103 patients (TI, n = 52; i-gel, n = 51). The not witnessed by ambulance staff group includes all cardiac arrests not witnessed by a trial paramedic. For the witnessed vs. not witnessed analyses, there were missing data for seven patients (TI, n = 3; i-gel, n = 4). For the initial ventilation success vs. no initial ventilation success analyses, there were missing data for 26 patients (TI, n = 3; i-gel, n = 23).

Complete-case analyses

Table 13 contains the details of mRS scores at 30 days/hospital discharge and longer-term mRS scores at 3- and 6-month follow-up (see also Appendix 1, Figure 24). At 3 and 6 months post OHCA, there were higher odds of a better functional recovery in the TI group than in the i-gel group [3 months: TI, 123/4199 patients with data (2.9%), vs. i-gel, 121/4636 patients with data (2.6%), OR 0.89 (95% CI 0.69 to 1.14; p = 0.35), ADP –0.51% (95% CI –1.18% to 0.16%; p = 0.14); 6 months: TI, 134/4212 patients with data (3.2%), vs. i-gel, 136/4661 patients with data (2.9%), OR 0.91 (95% CI 0.71 to 1.16; p = 0.43), ADP –0.39% (95% CI –1.08% to 0.30%; p = 0.27)] (see Table 13 and Figure 11).

Worst-case scenario sensitivity analyses

Summaries for worst-case longer-term mRS scores are presented in Appendix 1, Figure 25. The trends at 3 and 6 months in this scenario were the same as those in the complete-case analyses. There were higher odds of better functional recovery in the TI group than in the i-gel group [3 months: TI, 2.8%, vs. i-gel, 2.5%, OR 0.88 (95% CI 0.69 to 1.14; p= 0.34), ADP –0.49% (95% CI –1.13% to 0.15%; p = 0.13); 6 months: TI, 3.0%, vs. i-gel, 2.8%, OR 0.91 (95% CI 0.71 to 1.16; p = 0.43), ADP –0.37% (95% CI –1.03% to 0.29%; p = 0.27)] (Table 14; see Figure 11).

Imputed-case scenario sensitivity analysis

Multiple imputation of mRS score (3 and 6 months), single summary index (30 days/hospital discharge and 3 and 6 months) and EQ-5D VAS score (30 days/hospital discharge and 3 and 6 months) was performed. A total of 60 imputed data sets were created because the highest percentage of missing data was 60% of those who survived to 30 days/hospital discharge.

Summaries for imputed-case mRS score summaries are presented in Appendix 1, Figure 26. There were similar odds of a good functional recovery in the TI and i-gel groups at both 3 and 6 months [3 months: OR 1.00 (95% CI 0.83 to 1.20; p = 0.98), APD –0.13% (95% CI –1.20% to 0.94%; p = 0.81); 6 months: OR 0.98 (95% CI 0.81 to 1.18; p = 0.80), APD –0.26% (95% CI –1.33% to 0.82%; p = 0.64)] (Table 15; see Figure 11). These results support the results found in the complete-case and worst-case scenarios for mRS score.

Complete-case analysis

Crude responses to the five EQ-5D dimension questions showed that there were no clear differences between the two treatment groups considering the small number of patients who completed these forms (see Appendix 1, Table 41). The single summary index and VAS scores at 30 days/hospital discharge and 3 and 6 months post OHCA were completed by patients who had survived to these time points and consented to active follow-up only. The complete-case single summary index score and VAS score summaries at all three time points are presented in Appendix 1, Figures 27 and 28. The results are shown in Figure 12.

FIGURE 12.

Complete-case single summary EQ-5D index scores.

Table 16 contains the details of the single summary index and VAS scores at 30 days/hospital discharge and 3 and 6 months. There were higher median index and VAS scores at 30 days/hospital discharge in the TI group than in the i-gel group and there were similar median scores at the 3- and 6-month time points in both groups. There was a trend towards a higher odds of survival in the TI group than in the i-gel group at all three time points. For the QoL part of the model (‘score for survivors’), there was less consistency across the time points (Figure 13; see Table 16 and Figure 16).

FIGURE 13.

Complete-case VAS scores.

Worst-case scenario sensitivity analyses

Table 17 contains the results for the worst-case scenario single summary index and VAS scores at 30 days/hospital discharge and 3 and 6 months. The worst-case scenario summaries for single summary index and VAS scores are presented in Appendix 1, Figures 29 and Figure 30. The results of the formal statistical comparisons of worst-case single summary index and VAS scores are shown in Figures 14 and 15.

FIGURE 14.

Worst-case single summary index scores.

FIGURE 15.

Worst-case VAS scores.

As in the results of the complete-case analysis, for both single summary index and VAS scores, there was a trend towards a higher odds of survival in the TI group than in the i-gel group at all three time points. The ‘score for survivors’ part of the model showed less consistent trends (see Table 17 and Figures 9 and 14).

Imputed-case scenario sensitivity analyses

The results of the imputed-case scenario sensitivity analyses of the QoL outcomes are shown in Table 18. Appendix 1, Figures 31 and 32, shows the worst-case scenario summaries for single summary index and VAS scores. Figures 16 and 17 show the formal statistical comparisons of imputed-case single summary index and VAS scores.

FIGURE 16.

Imputed-case single summary index scores.

FIGURE 17.

Imputed-case VAS scores.

The imputed-case scenario analyses results showed a trend towards a better odds of survival in the TI group than in the i-gel group for both the single summary index and VAS scores at all three follow-up time points. The results of the QoL part of the model (‘score for survivors’) showed less consistent trends (see Table 18 and Figures 16 and 17).

Trial conduct

The design and implementation of the AIRWAYS-2 trial was informed by a growing, but still limited, body of evidence from previous out-of-hospital RCTs35,81 and a substantial feasibility trial. 25 AIRWAYS-2 was a large and complex trial that aimed to guide future paramedics’ airway management in patients with OHCA. Research in the emergency setting is challenging, but it is essential if we are to improve future clinical practice. We identified a widespread lack of familiarity with pre-hospital research. Many hospitals had no experience of participating in paramedic studies or of approaching patients for consent after they had been enrolled in a trial outside hospital. 26

Blinding of paramedics was not possible; this presented a challenge because it required a trial design that ensured inclusion of all eligible patients attended by a participating paramedic. The only way to achieve this was to enrol eligible patients automatically. To enable this, the investigators gained approval for the collection and retention of a minimal data set without consent. Legal provisions enable research in an emergency setting, providing all proposed activities have approval from an appropriate REC. 82 The ethics committee demonstrated a high degree of understanding of the nature of pre-hospital research. This may have been promoted by recent increases in research activity by EMS and previous work completed by our team. 25 Crucially, our trial design and ethics application was supported by an active and well-informed patient and public research advisory group comprising OHCA survivors, their families and other members of the public.

In most clinical trials, research activities are performed by clinicians who have research-specific training and experience. Most of the paramedics who participated in the AIRWAYS-2 trial had little or no previous exposure to clinical trials. They were nevertheless required to conduct several research-related activities without compromising patient care following a relatively short period of face-to-face and online training. 83 The scene of an out-of-hospital resuscitation attempt for a patient in cardiac arrest is an uncontrolled and challenging environment in terms of patient, scene and team management. The difficulties of recognising eligibility, conducting interventions and reporting patients during and after such events are likely to have had an impact on overall trial performance. However, the successes of the research are a testament to the commitment of the participating paramedics who nonetheless delivered the trial.

The AIRWAYS-2 trial used a cluster randomised design, which has strengths and weaknesses. At the start of the trial, we considered alternative approaches to randomisation. Airway management is a very early step in the management of OHCA by paramedics and occurs in unpredictable, high-stress environments. We were concerned that any attempt to randomise patients individually (for example, using sealed opaque envelopes, or a telephone or web-based randomisation service), although technically possible, would carry an unacceptable risk of treatment delay because any randomisation process would distract paramedics from direct patient care. For a significant proportion of patients enrolled in the AIRWAYS-2 trial (1164/5888; 19.8%), the cardiac arrest occurred in the presence of ambulance staff (EMS witnessed) and randomisation procedures would be particularly problematic for this group because the attending paramedic would have no time to prepare.

Cluster randomisation at the level of the paramedic was supported by our patient and public research advisory group, which was focused on the need for paramedics to deliver high-quality care in an emergency rather than engage in research procedures. This led us to a cluster randomised design, and we elected to continue the approach that we had used successfully in our REVIVE-AIRWAYS feasibility study39 by randomising individual paramedics. We considered using larger randomisation clusters (for example, by ambulance station); however, this would have increased the intra-cluster correlation and require an inflation of an already large sample size with associated costs.

The Pragmatic Airway Resuscitation Trial (PART)53 used a crossover design, which we considered; however, it was deemed impractical to retrain all paramedic participants during the study, with the associated risk of undermining protocol compliance and trial delivery. The PARAMEDIC-2 trial84 was able to randomise patients individually; however, this was facilitated by the fact that PARAMEDIC-2 was a double-blinded drug trial in which paramedics were required to open a pre-prepared pack and give the drug it contained; furthermore, randomisation in PARAMEDIC-2 occurred later in the OHCA, providing more opportunity for the paramedic to prepare (physically and cognitively) for enrolment. Finally, the CAAM trial85 of BMV versus TI in OHCA was able to achieve individual patient randomisation; however, this also occurred later in the OHCA and was undertaken by doctors who usually arrived after earlier EMS responders had undertaken initial airway management; indeed, one of the criticisms of the CAAM trial is that relatively late enrolment reduced the likelihood that the intervention would influence outcome.

However, the use of a cluster randomised design in the AIRWAYS-2 trial had considerable drawbacks. Foremost among these was the lack of allocation concealment, which created a substantial risk of selection bias. To avoid paramedics selectively enrolling patients, we therefore opted to automatically enrol, under a waiver of consent, every eligible patient. The processes that were put in place to achieve this proved to be very labour intensive but successful. 26 However, enrolling all eligible patients had the additional effect of including a significant number of patients who did not receive the trial intervention or crossed over to the alternative AAM strategy, with resulting protocol non-adherence. This was further exacerbated by the requirement to allow paramedics an element of clinical freedom to adapt their approach to prevailing circumstances to assure patient safety. The analysis and interpretation of the trial results became more complex as a result. We believe that the findings of our whole-group ITT and instrumental variable analyses are robust; however, in these circumstances any per-protocol approach should be treated with extreme caution.

The number of paramedic clusters in each group was relatively equal (TI, n = 696; i-gel, n = 686). However, the number of patients randomised by the paramedic clusters in those groups was not equal (TI, n = 4410; i-gel, n = 4886). This can be partly explained by a variation in the median number of patients enrolled per paramedic (TI, n = 5; i-gel, n = 6). There was also a small number of paramedics in the i-gel group who enrolled a disproportionately large number of patients, with a maximum of 56 patients enrolled, compared with a maximum of 48 patients in the TI group. These ‘super-enroller’ paramedics were small in number. It is likely that the different patient group sizes are because of a chance imbalance in the allocation of the ‘super-enrollers’ that favoured the i-gel.

Paramedics randomised to use TI were less likely to use any form of AAM than paramedics randomised to use the i-gel. TI is a more complex skill than SGA insertion and requires two practitioners, additional equipment and good access to the patient’s airway. 86 However, OHCA often occurs in locations where patient access is challenging. It seems likely that the increased complexity of TI influenced the paramedics’ behaviour so that they were less inclined to proceed with AAM if they had been randomised to the TI group than to the i-gel group. This is a pragmatic reflection of actual clinical practice, which resulted in an imbalance in the proportion of patients who received any form of AAM between the two groups. Interestingly, despite the fact that patients allocated to TI were less likely to receive AAM, this did not translate into worse outcomes, suggesting that AAM in any form, provided early in OHCA, may not improve outcomes in cardiac arrest. This is consistent with a recent European RCT85 that did not detect a difference in outcome between patients allocated to TI or basic airway management during OHCA.

We believe that, for trials of non-drug interventions delivered very early in OHCA, cluster randomisation will continue to be required to ensure that randomisation procedures do not delay essential clinical treatment. However, this should be reviewed in the light of ongoing digital and technological developments that may facilitate near-instantaneous patient randomisation in the future. Where cluster randomisation is used and concealment is impossible, strenuous efforts to avoid selection bias, combined with whole-population ITT and/or instrumental variable analyses, should be employed.

Adherence to the trial protocol differed between the two treatment groups, with higher adherence in the i-gel group than in the TI group (82.1% compared with 61.9%) (see Chapter 4, Additional analysis). The higher adherence to the i-gel may reflect paramedic preferences for this device, and ease of use. For an illustration of interventions received by patients, see Figure 7. Rates of AAM use in patients who did not have ROSC on paramedic arrival are also different between the two treatment groups.

Despite considerable effort by the research teams, only 52.4% of survivors consented to active follow-up (see Figure 4), which is lower than observed in some other OHCA trials. 84,85 There are several potential explanations for this. Owing to the trial design and waiver of consent, patients could not be asked to consent to participate in the trial (since the intervention had already occurred). Instead, they were asked to consent to either active or passive follow-up. The lower consent rate could be the result of a lack of perceived benefit to the individual as a result of participating. 87 It may also be related to the patient’s condition, cognitive impairment post OHCA or a feeling of being overwhelmed by other clinical activities required at that time. Several strategies were proposed and adopted to look to increase the active follow-up consent rate. The trial’s patient and public research advisory group advised that we review and refine the timing of the approach for consent. It was agreed that patients should be informed of the trial and approached for consent shortly after they were discharged from the ICU or CCU, but before hospital discharge. It was recommended that all participants receive an in-person approach and invitation to consent prior to discharge from hospital, wherever possible. Seeking consent at this time and in this manner was complex and required the local research teams to carefully monitor the location and capacity of patients recovering from OHCA. This resulted in some patients being discharged from hospital before being approached. When this happened, we requested written consent by post, but this method of requesting consent resulted in a low rate of consent to active follow-up (44.2%). Other recommendations to improve the consent rate included providing a range of contact options for patients, including telephone, e-mail and postal contact details for the local research team and trial co-ordinating centre. The trial team also worked to ensure that consent and active follow-up processes were as clear and streamlined as possible.

Because interruptions in chest compressions during TI have been identified as potentially harmful in OHCA patients,13 we aimed to measure chest compression fraction as a measure of CPR quality. However, use of the compression fraction cards was low, with only a few readable cards returned (see Chapter 4, Chest compression fraction). The cards returned did not show any significant difference in chest compression fraction between the two treatment groups. However, the small numbers mean that there is considerable uncertainty in this result. Encouragingly, the chest compression fraction was comparatively high in the AIRWAYS-2 trial, indicating that good-quality basic life support was delivered by ambulance staff. Chest compression fraction is not routinely measured in OHCA practice or research in the UK, but has been recognised internationally for more than a decade. 36 In retrospect, the use of an additional and separate device may have been impractical for paramedics already participating in the AIRWAYS-2 trial, and more automated approaches to the measurement of chest compression fraction (for example through defibrillator electrodes) should be considered in future trials.

Longer-term secondary trial outcomes and the health economics analyses for this trial use data collected routinely and obtained through NHS Digital. Using routinely collected data enables the trial to undertake more substantial analyses in an efficient way without placing a large burden of direct data collection and entry on local hospital teams, and has enabled the AIRWAYS-2 trial to be one of the largest health economics analyses of OHCA patients completed to date. However, the application process to obtain these data took almost 3 years from initial submission to receipt of data. The application was complicated by several issues, including NHS Digital system challenges and staff changes, the introduction of both the General Data Protection Regulation88 and Information Governance Toolkit,89 protracted contract sign-off periods and the requirement for an amendment to the trial’s CAG approval. The delays to the application process meant that the trial team were unable to obtain an extract of routine data part-way through the trial and ultimately had to apply for extensions to the funder’s final report deadline to include the full secondary outcomes and health economics analyses. When data were received, some problems were identified in one data set that could not be resolved before submission of this report (see Chapter 2, Availability of resource use and cost data).

Trial results

In this pragmatic cluster RCT comparing a strategy of initial AAM with the i-gel versus TI, there was no significant difference in the primary outcome of favourable functional outcome after OHCA. Owing to the large sample size and randomised design, these findings are likely to be generalisable to the wider population of adult, non-traumatic OHCA when attended by NHS paramedics in England.

Paramedics are less likely to provide AAM (TI, SGA or some other method) to patients with a short duration of cardiac arrest or who receive bystander resuscitation and/or defibrillation. These patients are also considerably more likely to survive. 90 This relationship, causing confounding by indication, is an important limitation of many large observational studies that show an association between AAM and poor outcome in OHCA. 91 The phenomenon of resuscitation time bias has been well described. 90 In our trial, 21.1% (360/1704) of patients who received no AAM achieved a good outcome, compared with 3.3% (251/7576) of patients who received AAM.

At the outset, it was expected that most patients with a favourable outcome would not receive AAM and that some crossover would occur. For these reasons, two pre-specified exploratory sensitivity analyses (ITT and as treated) were undertaken in only those patients who received AAM, even though these analyses are susceptible to bias. 27,92 Patients who received AAM were similar in the two groups (see Appendix 1, Tables 33 and 34), and a strategy of i-gel first was associated with better outcomes whenever AAM was undertaken by a trial paramedic (see Appendix 1, Table 35). However, the difference between groups was less than the pre-specified clinically important difference of 2% and less than the minimum important difference of ≈ 3% reported by others. 23 The i-gel-first strategy also achieved initial ventilation success more often, with no increase in the overall rate of reported regurgitation and aspiration, although the i-gel was significantly more likely to dislodge after successful placement than a tracheal tube. 27

As described, these two exploratory analyses were subject to bias because patients who did not receive AAM were excluded and there was differential crossover in the two groups. In the light of this, a causal analysis was undertaken. The causal analysis included all trial participants and took account of the treatment received, the randomised allocations and the fact that a single paramedic could deliver the i-gel intervention but two paramedics were required for TI. The standard airway management strategy meant that paramedics had to wait for another paramedic before they could deliver TI. This meant that the number of paramedics on scene could determine a certain amount of the crossover present. Thus, the causal analysis was not subject to the same biases as the exploratory sensitivity analyses. Moreover, given that this analysis takes into account the differential adherence in the two groups, it better reflects the true level of uncertainty in the difference in outcome between the two treatment groups than the primary ITT analysis. The result of this causal analysis favoured a strategy of TI first, but with a wide 95% CI (–5.38% to 4.40%) for the treatment effect. However, while the 95% CI for ITT excluded the pre-specified clinically important 2% difference, the causal analysis does not rule out the possibility of a difference of this magnitude or higher.

A recent RCT of OHCA patients in France and Belgium tested the non-inferiority of BMV compared with early TI, with both interventions delivered by physicians as part of a pre-hospital team. The non-inferiority margin was 1% mortality. The trial was inconclusive in that it failed to establish the non-inferiority of BMV compared with TI. 85 To our knowledge, no RCT has compared BMV with a SGA in patients with OHCA. Reported rates of ventilation and TI success have been higher in previous studies,85,93,94 but these have been based on selected populations and practitioners with greater training and experience, including physicians. This trial reflects both the pragmatic reality of current paramedic practice in England and the challenges of airway management in a patient group where regurgitation and poor airway access are common. 27

The recent cluster crossover PART53 of North American patients with OHCA randomised 27 EMS to an initial strategy of using a different SGA (the laryngeal tube) or a strategy of using initial TI. The trial showed that a strategy of initial SGA insertion had significantly greater 72-hour survival rates than an initial strategy of TI. A key difference in the design of PART compared with the AIRWAYS-2 trial is the exclusion of patients judged not to require AAM. The AIRWAYS-2 trial included all patients with OHCA, irrespective of the perceived need for AAM, to avoid the risk of bias due to paramedics making different judgements about the need for AAM conditional on knowing the method of AAM to which they were allocated. In PART, it is not clear how the researchers avoided the risk of this bias, although there was little evidence that patients in the SGA and TI groups differed.

As in the AIRWAYS-2 trial, an initial strategy of SGA first also achieved higher initial ventilation success in PART. However, rates of regurgitation and aspiration during or after AAM were not reported. Following a recent systematic review of AAM in cardiac arrest,95 the International Liaison Committee on Resuscitation (ILCOR) published treatment recommendations on this topic. 96 In settings with a low TI success rate (the intubation success rate of 70% documented in this trial would be deemed low), ILCOR suggests using a SGA instead of TI for OHCA.

Loss of a previously established airway occurred twice as frequently in the i-gel group as it did in the TI group. There are some cardiac arrest patients in whom effective ventilation cannot be achieved with basic airway management techniques or a SGA and in whom TI may be the only way of achieving effective ventilation. The exact role of different AAM techniques in adults with OHCA, and the associated implications for skill acquisition and maintenance, remain to be determined. 27

The 3- and 6-month outcomes from the trial were very similar to the primary outcome measured at hospital discharge (or 30 days if sooner). 27 There was no significant difference in either the primary outcome of mRS score or the EQ-5D measure of HRQoL between the two groups at 3 and 6 months. The worst-case and imputed-case sensitivity analyses, designed to determine the potential effect of missing data, did not alter our findings.

Most clinical trials in OHCA have reported short-term outcomes only, and even the most contemporary international advisory statement describing a core outcome set for clinical trials in OHCA patients does not recommend data collection beyond 90 days, mainly because of the substantial resources required and the risk of attrition bias. 97 As a result, the natural history of survivor recovery following OHCA has been documented by only a few investigators,98–101 and there remains a need to examine the longer-term impacts of OHCA on functional status, cognition and QoL. 102,103

Several studies have documented improvements in the functional status of OHCA survivors for at least the first 3 months and up to 6 months after cardiac arrest. 101,102 Our data support this: we have shown a substantial shift in the distribution of mRS scores consistent with improving functional status between hospital discharge and 3 months, and a smaller shift in the same direction between 3 and 6 months. The number of patients with a mRS score of 5 (severe disability) shows a substantial decrease between hospital discharge and 3 months, which likely represents a combination of some patients dying (mRS score of 6) and others improving their functional status. 104

Although PART53 documented a significantly higher rate of favourable neurological outcomes among patients randomised to a strategy of initial laryngeal tube compared with TI, longer-term outcomes have not been reported, so it is unknown if this difference would have been sustained at 3 and 6 months.

Health economics

The main findings from the economic evaluation are that there is very little difference between the groups in either costs or effects and great uncertainty around the cost-effectiveness results. There was very little difference in total costs per patient between the two groups. Patients in the TI group had costs, on average, £157 less than those in the i-gel group. This difference largely relates to slightly lower intensive care costs in the TI group. Varying unit costs in sensitivity analyses had very little impact on mean cost differences, reinforcing the finding that resource use was similar between groups. Nine patients had total costs exceeding £100,000, including one patient in the TI group with total costs of £271,014; these patients exerted a modest impact on cost results but did not alter conclusions. Although only 20% of patients survived to hospital admission, inpatient and intensive care costs were the key drivers of total costs; therefore, it is disappointing that the HES critical care data set could not be used to cost time in intensive care.

The QALYs gained in each group are small, influenced by the large proportion of patients who died at an early stage in the trial and who contribute a tiny negative gain to QALYs. Sensitivity analyses around alternative assumptions for outcomes (assuming a baseline utility of zero rather than a negative value, and considering life-years rather than QALYs) did not affect the differences between the groups. The difference between the groups for QALYs is particularly small, creating a very small denominator for the ICER. Dividing the difference in costs by a tiny number, close to zero, resulted in a very large ICER (–£102,362). The point estimate in the base-case analysis suggests that TI is dominant over the i-gel because it is both more effective (very slightly greater QALY gain) and less costly and, therefore, cost-effective. The CEAC suggests that the i-gel is unlikely to be cost-effective. However, there is a great deal of uncertainty around these results. The point estimate is close to the origin and the bootstrap replicates of the cost and QALY differences cover three quadrants of the cost-effectiveness plane; in reality there is no evidence to suggest any difference between the groups.

Strengths

To our knowledge, the AIRWAYS-2 trial is the largest RCT of airway management in OHCA to date, assessing a primary outcome of key importance to patients, clinicians and health services, adequately powered for a clinically important target difference, accompanied by a cost-effectiveness analysis and including features to minimise the risk of bias. The latter included (1) automatic enrolment, allowing us to include all eligible patients while assessing whether or not paramedics adopted a different threshold for resuscitation conditional on knowledge of their allocation and (2) blinded assessment of outcome beyond the ED. We obtained the primary outcome for 99.9% of enrolled patients. These two factors combined mean that the primary result has high validity.

Trial limitations

This trial has several limitations. First, there was an imbalance in the number of patients in the two groups, probably because of unequal distribution of a small number of ‘super-enroller’ paramedics in the two groups; it was not possible to stratify for this because ‘super-enroller’ paramedics could not be identified in advance. Second, there was crossover between groups, which was inevitable on practical and ethics grounds. Third, although other elements of care (e.g. initial basic airway management and subsequent on-scene and in-hospital care, such as targeted temperature management and access to angiography) followed established guidelines, differences in these factors between groups could have influenced the findings. Fourth, the participating paramedics were volunteers, and their airway skills may not be representative of those who chose not to take part. Fifth, the findings are applicable to use of the i-gel in countries with similar EMS provision to England, where paramedics attend most OHCAs. The findings may not be applicable in countries with physician-led EMS provision or to other SGAs, which may have different characteristics. However, the principles underpinning the insertion and function of all SGAs are similar. 27 A further limitation was that the degree of clustering was much greater than anticipated. An intracluster correlation of 0.05 (all other sample size inputs remaining unchanged) meant that we had 83% power rather than 90% to detect a difference of 2%.

In keeping with similar studies, our trial had relatively few survivors from whom to gather longer-term outcomes. Furthermore, we were reliant on both active patient consent and co-operation at 3 and 6 months to collect the required mRS and EQ-5D data. Despite considerable effort by the research teams, only 52.4% of survivors consented to active follow-up. As a result, our analyses are undermined by missing data, with limited power and the risk of attrition bias. However, the proportion of missing data was very similar in the two groups, and there was no evidence that the availability of follow-up data was influenced by patient allocation. Furthermore, the sensitivity analyses did not alter our findings to any significant degree.

Pre hospital

In the pre-hospital phase, a series of dates and times were collected: time each ambulance arrived at the scene, time of death or time the patient left the scene for hospital, and time of arrival at hospital. These data were used to calculate the duration spent by ambulance staff with patients. For each paramedic attending an AIRWAYS-2 patient, the time from arrival at the scene of the OHCA to the time they took the patient into hospital (or the time the patient left the scene if transported in another vehicle), or until time of death if the patient died at the scene, was calculated. Where this generated implausible durations with the patient, such as negative durations of ≥ 10 minutes, details of all staff and vehicles attending the patient were reviewed manually to identify typos in the series of dates and times. Negative durations of < 10 minutes were assumed to be paramedics arriving too late to assist, unless the paramedic was arriving > 1 hour after the first paramedic on scene, in which case details were reviewed manually. The series of dates and times were reviewed manually for durations > 3 hours to correct typos and/or check that this was plausible against the other times recorded. Time at the scene after a patient’s death (awaiting police, for example) or after a patient had left for hospital in another vehicle was not costed.

Intensive care unit stays

Dates and times of initial admission to ICU, discharge from ICU or death in ICU were captured on the trial CRFs. Dates were complete for all patients; mean imputation was used to handle five missing times. Additional time in ICU for patients subsequently re-admitted to ICU later in their index admission was available for patients who had consented to the trial only.

Hospital Episde Statistics data sets: emergency medicine, admitted inpatient care and non-admitted consultations

The three HES data sets for ED attendance, inpatient care and outpatients visits were cleaned and inputted into the HRG4+ 2017/18 Reference Costs Grouper (NHS Digital108). This produced Healthcare Resource Group (HRG)/service codes for each activity, which were then costed using NHS Reference Costs 2017/18. 62

For admitted inpatient care, one of the inputs the grouper requires is the number of days spent in ICU for that episode of care. ICU care is costed separately, but days in ICU need to be excluded from the length of stay for an episode to correctly calculate any additional bed-days to be costed beyond a standard length of stay for that HRG code (known as excess bed-days). The initial ICU length of stay from the trial CRFs was merged into this HES data set and the days split through one or more episodes of care for the initial inpatient stay. Given the complexity of the data set, and missing data for patients who did not consent, it was not possible to merge time in ICU beyond the initial stay into the admitted inpatient care data set.

For each of the data sets, duplicate records were dropped. Non-identical records with the same date for ED attendance and the same date and speciality for outpatients appointments were assumed to be duplicates, and one was dropped. Only those outpatient appointments that the patients attended were costed.

Multiple imputation

The following cost components were imputed for initial care: pre hospital, ED attendance, inpatient care, subsequent intensive care days. The following cost components were imputed for the follow-up period to 6 months: ED attendance, inpatient care, outpatients visits, community care up to 3 months and community care from 3 to 6 months. These cost components were imputed together with the three EQ-5D scores; the complete variables age, sex and ambulance trust; initial ICU length of stay; indicator variables for whether or not the patient survived to the ED and for alive at 6 months; and a time alive variable, separately by treatment group. The time alive variable was either days to death or 183 days for patients who survived to 6 months. Each variable was imputed conditional on being alive at that stage. Prediction mean matching with 10 nearest neighbours was used (so, based on the variables included, the 10 most similar patients were identified and the costs for one randomly selected patient assigned to the patient with missing data).

Survival status to 6 months was unknown for 11 patients in the trial: 10 patients who survived to hospital discharge (five in each group) and one patient who survived to 3 months. To accommodate these patients in the imputation, they were assigned a weighted average of time in follow-up/time to death of patients who survived to hospital discharge and 3 months.

Figures 33 and 34 compare the observed total costs for patients with complete data and total costs for all patients, respectively, based on the imputed data. Given the skewed nature of the distributions, the figures are split into two so that the shape of the distribution can be seen more clearly. The outer figures show the total costs for patients with costs ≤ £20,000; the inset figures show the patients with costs > £20,000. The figures of imputed data reflect what is known of patients with missing costs; the larger number of patients with low costs reflects those who died early on in the trial who were missing the cost of airway devices only, and the heavier positive tail reflects the many patients with high resource use who were missing total costs.

FIGURE 33.

Observed total costs. The outer figure shows the total costs for patients with costs ≤ £20,000; the inset figure shows the total costs for patients with costs > £20,000.