Adrenaline to improve survival in out-of-hospital cardiac arrest: the PARAMEDIC2 RCT

Chain of survival

The chain of survival9 concept (Figure 1) is recognised internationally and summarises the key components of the response to OHCA to optimise the chances of survival. The links in the chain are discussed in more detail in the following sections.

FIGURE 1.

The chain of survival. 9 CPR, cardiopulmonary resuscitation. Reprinted from Resuscitation, Vol. 71, Nolan J, Soar J, Eikeland H, The chain of survival, pp. 270–1, Copyright 2006, with permission from Elsevier.

Reprinted from Resuscitation, Vol. 71, Nolan J, Soar J, Eikeland H, The chain of survival, pp. 270–1, Copyright 2006, with permission from Elsevier.

Mechanisms by which adrenaline may cause harm

There are a number of mechanisms by which adrenaline may cause harm. These can be considered under the following headings.

Primary objective

The primary objective of this trial was to determine the clinical effectiveness of adrenaline in the treatment of OHCA, measured as a primary outcome of 30-day survival.

Secondary objective

The secondary objectives of the trial were to evaluate the effects of adrenaline on survival and on the cognitive and neurological outcomes of survivors, and to establish the cost-effectiveness of using adrenaline.

Pilot trial

An internal pilot was run to test that the components of this trial worked together. This pilot ran for 6 months. The data from this were included in the main trial. During the pilot, we measured recruitment rate and compliance with the allocated intervention, and checked that the approach to data collection and follow-up worked effectively. The pilot phase ran seamlessly into the main trial. The results of the pilot trial were reviewed with the Trial Steering Committee (TSC), the Data Monitoring Committee (DMC) and representatives from the Health Technology Assessment (HTA) programme, specifically considering the achievement of the following targets:

• 25% of ambulance staff trained [i.e. the majority (80%) of participating staff at 25% of stations]

• 181 patients recruited within 6 months of first randomisation

• data available on primary outcome – > 98%

• proportion of patients who are alive agreeing to follow–up – > 75%

• reconcile IMP packs with participants enrolled in the trial

• review of the approach to inform patients and relatives of trial participation

• review of feasibility to collect secondary outcomes.

All pilot objectives were achieved, and the TSC approved continuation to the main phase of the trial on 7 May 2015.

Reasons for changes to the trial design

Inclusion criteria

Patients were eligible if both the following criteria were met:

• cardiac arrest in an out-of-hospital environment

• advanced life support initiated and/or continued by an ambulance service clinician.

Exclusion criteria

The exclusion criteria at the time of arrest were as follows:

• known or apparent pregnancy

• known to be or apparently aged < 16 years

• cardiac arrest caused by anaphylaxis or life-threatening asthma

• adrenaline given prior to arrival of ambulance service clinician.

In London Ambulance Service, traumatic cardiac arrests were also excluded, in accordance with local protocols.

Post-randomisation withdrawals and exclusions

There were three main sources of post-randomisation withdrawal and exclusions. The first was when, between randomisation (opening the drug pack) and administering the trial intervention, a patient was identified as ineligible. Examples of this include when a patient achieved ROSC, when a patient was confirmed to have died or when a trial exclusion became known to the ambulance clinicians before drug administration. This group would not receive vasopressor drugs in clinical practice. No follow-up data were collected on this group of patients and they were identified in the Consolidated Standards of Reporting Trials (CONSORT) flow diagram as post-randomisation exclusions.

The second situation is when, after drug administration, it subsequently became known that the patient was ineligible for the trial. An example of this would be discovering in hospital that the cause of the cardiac arrest was anaphylaxis. This group of patients would be exposed to the vasopressor drugs in clinical practice, as it is not until after drug administration that the exclusion is discovered. This group of patients were followed up in the normal manner and included in the intention-to-treat analysis.

The third scenario is when a patient or their legal representative withdrew their consent for ongoing data collection. This group of patients were eligible for and received the trial intervention, but incomplete data were obtained on their long-term outcomes. This group of patients were included in the intention-to-treat analysis, up until the point of withdrawal. The information sheet explained the trial and the data that were collected. The consent form separated out the different data that were collected, and gave the patient the option to decline. NHS records were continually used unless the patient explicitly refused permission for this, as were tracking of the patients via NHS Digital to determine survival to 12 months post cardiac arrest.

In the rare situation in which a patient had neither consented to nor refused follow-up, they were not included in the face-to-face follow-up, but data collection from NHS records and in-hospital data sets continued.

Methods for ensuring blinding

The packaging and the labelling of the IMP packs did not reveal which IMP was being used; therefore, the patient, attending clinicians, hospital treating team, research paramedics and trial administration team were masked to treatment allocation. Only the statistician was able to link the IMP pack number to the allocation of adrenaline or placebo.

Methods for unblinding the trial

The chief investigator retained the right to break the code for serious adverse events (SAEs) that were unexpected and suspected to be causally related to an investigational product, and that potentially required expedited reporting to regulatory authorities. The chief investigator unblinded if requested to do so by a coroner as part of a death enquiry. In exceptional circumstances, the chief investigator also considered requests for unblinding from patients or, if they lacked capacity, family members/next of kin. In this scenario, the trial statisticians made the unblinding on the chief investigator’s request and the chief investigator was informed accordingly of the allocation. This occurred only if the request was made after the benefits and harms of disclosing this information to them had been discussed. Otherwise, treatment codes (IMP pack number) were broken only for the planned interim analyses of data by the statistician at the request of the DMC.

Methods for unblinding the trial: after trial completion

Requests for unblinding of treatment allocation were received (either from survivors or from the next of kin of trial participants who were deceased) after completion of the trial. When these requests were received, the PARAMEDIC2 trial office sent the enquirer (on behalf of the ambulance services) an information sheet about unblinding and a response form for completion if they wished to continue with unblinding after having read the information provided. Once a completed response form was received, requesting unblinding, the PARAMEDIC2 trial office responded, once checks had been performed to verify the case details, to confirm the treatment allocation on behalf of the ambulance services, with ambulance service contact details for further queries.

Efficacy

Health economics

Incidence of primary outcome

Most existing data refer to survival to hospital discharge rather than survival to 30 days, but as most mortality will occur in the first few days after cardiac arrest, we expect these two measures to be very similar. Estimates of long-term survival of patients who receive adrenaline during a resuscitation attempt vary between about 3.5% and 12%. From national data for England, overall survival to hospital discharge of patients for whom resuscitation is attempted is 7%. 89 However, this will include a small number of patients who achieve ROSC immediately and would not receive adrenaline, and hence would not be recruited to the trial. As these patients have much better outcomes, we expected that the survival among the trial population would be slightly lower. Estimates from the Norwegian trial of i.v. drugs and the Australian trial of adrenaline were 9%57 and 4%,56 respectively. We therefore expected a rate of survival to 30 days of ≈ 6% in the adrenaline group.

The trial’s primary aim was to estimate the treatment effect of adrenaline and the uncertainty around this; we therefore based the target sample size primarily on the precision of the estimate of the risk ratio (RR). 40 Figure 5 shows the precision that is achievable (width of the 95% CI for the RR) with different total sample sizes, for RRs (placebo vs. adrenaline) of 1.25 and 1.00. A RR of 1.25 corresponds to an increase in 30-day survival from 6% in the adrenaline group to 7.5% in the placebo group.

FIGURE 5.

Width of 95% CI for the RR against sample size. (a) RR 1.25; and (b) RR 1.0, with 6% survival in the adrenaline arm.

Sample size

The target sample size was 8000 participants, which was expected to give a width of the 95% CI for the RR of approximately 0.4 or slightly less; for a RR of 1.25, the 95% CI would be 1.07 to 1.46, and for a RR of 1.0 the 95% CI would be 0.84 to 1.19. There was a trade-off between precision and practicality in setting a target sample size at > 8000, there was only a small improvement in precision, but the difficulty and time needed to recruit this number increased significantly. We expected a very small number of missing data for survival outcomes. In the PaRAMeDIC trial,102 we ascertained survival status for > 99% of randomised patients; therefore, we have not adjusted the sample size estimates to account for missing data.

Using a conventional sample size calculation based on a significance test, a sample size of 8000 would have 93% power to achieve a statistically significant (p < 0.05) result if the true treatment difference is a RR of 1.33 (increase from 6% in the adrenaline group to 8% in the placebo group), or 75% power if the true treatment difference is a RR of 1.25 (increase from 6% in the adrenaline group to 7.5% in the placebo group).

Reconsideration of sample size after low survival rate

In July 2016, the DMC raised concerns regarding a lower than anticipated survival rate. We explored additional data sources and the current literature to assess if the original assumption was correct. Since the inception of the trial, we had access to two contemporary sources of information for the epidemiology and outcome of this patient group in the UK.

The first was a secondary analysis of the PaRAMeDIC trial. 102 The PaRAMeDIC trial102 enrolled adult patients experiencing OHCA in three English and the Welsh ambulance service regions. Patients were eligible for enrolment if they had an OHCA attended by a trial vehicle and resuscitation was continued by the EMS team. Patients who were pregnant or who sustained a traumatic cardiac arrest were excluded. We collected information on whether or not a patient received i.v. cardiac arrest medications per se, rather than specifically adrenaline. As resuscitation algorithms recommend that adrenaline and amiodarone (the only other recommended i.v. drug for cardiac arrest) are given together, we believed that this was a reasonable surrogate to the patient requiring i.v. adrenaline. For the PaRAMeDIC trial,102 this group comprised 3621 patients, with an overall 30-day survival rate of 2.8%.

The second source of data was the national OCHA registry (OHCAO) hosted by the University of Warwick. 103 This registry collects process and outcome information from all English ambulance services. Data were available covering the period from 2013 to 2015. These data were analysed for patients aged > 16 years who were given i.v. adrenaline (n = 28,939). In this group, 3.1% survived to discharge.

We extended the initial review of the literature to include studies that included standard-dose adrenaline as control, rather than limiting to intervention. Table 2 gives a brief detail of these studies, together with the percentage rates for survival to discharge for patients receiving standard-dose adrenaline (1 mg). This identified 10 studies in which high-dose adrenaline or vasopressin were given as comparator. In one trial, placebo was given as comparator. 56 The median rate of survival to discharge was 2.8%, and the weighted mean was 3.5%.

Considering this information and the survival outcomes for PARAMEDIC2 at the time of our review, we concluded, as a trial team, that our initial estimates of survival to discharge/30-day survival, as detailed in the protocol, were overly optimistic. An adjusted sample size calculation based on the collected data indicated that, if we assumed a rate of survival to 30 days of 2% in the control arm, we would need > 24,000 patients for a RR of 1.33 at 90% power.

In addition, we estimated treatment effects detected by the sample size of 8000, as seen in Table 3.

We believed that revising the sample size to 24,000 was unachievable (and unaffordable) at that point in the trial.

We noted that the Jacobs et al. 56 trial showed an OR of 2.2 in the survival to discharge outcome, but with wide CIs (95% CI 0.7 to 6.3). Furthermore, a threshold of 1% in absolute risk reduction for outcomes has been used widely in resuscitation science as the threshold that defines the minimal clinically important difference. 114,115 We therefore believed that the trial would still yield valuable information about the safety and effectiveness of adrenaline if the observed survival rates continued to the end of the trial.

Obtaining consent

The ambulance service research teams received training on informed consent and assessing capacity, good clinical practice (GCP) guidelines, relevant legislation, and the trial-related procedures around consent.

Enquiries regarding trial participation

The following process was introduced at the end of the trial to deal with trial participation enquiries from members of the public.

If a member of the public enquired as to whether or not their next of kin was enrolled in the PARAMEDIC2 trial, they completed a trial participation enquiry form. On receipt of a completed trial participation enquiry form, the PARAMEDIC2 trial office worked with the appropriate site to check whether or not the next of kin of the enquirer was enrolled in the PARAMEDIC2 trial. Once it was confirmed, a letter was sent from the appropriate ambulance service to confirm whether or not the enquirer’s next of kin was enrolled in the trial, along with an information sheet about the trial, which included contact details for the PARAMEDIC2 trial office.

Screening data

Data were collected on a screening log of all cardiac arrests, which were attended by a trial-trained paramedic in the trial areas. These data consisted of the case identifier, the age and sex of the patient and the reason why the patient was not enrolled in the trial. This allowed assessment of the proportion of missed enrolments and the reasons, to ensure that the trial sample was representative of the trial population. The reasons for missed enrolments were established either from reviewing the patient’s clinical record, or from speaking to the attending clinician. Several strategies were used during the trial to reinforce the message that all eligible patients should be enrolled in the trial, and data on the numbers and reasons for missed enrolments were reviewed throughout the trial and fed back to sites.

Patient enrolment

All cardiac arrests for which a trial pack was opened were reported to the ambulance service trial teams by the recruiting clinician. The method for notification of enrolled patients was specific to each research site, but was usually done via telephone to the control centre or to a dedicated telephone number. Once ambulance service research teams were notified of an enrolled patient, the patient details were registered promptly on the trial database via an online web application hosted by the University of Warwick.

Baseline cardiac arrest data

Baseline cardiac arrest data were obtained retrospectively from ambulance service clinical records and the OHCAO registry (University of Warwick) and transcribed directly onto eCRFs via the PARAMEDIC2 web application. All ambulance service staff were trained on how to collect and enter trial data, and all data definitions followed Utstein recommendations. 92 Follow-up data were then obtained from hospitals, general practitioner (GP) surgeries, NHS Personal Demographics Service and patient follow-up questionnaires and were entered into the PARAMEDIC2 web application as they became available.

Hospital

Patients were taken to any hospital in the trial regions. Although hospital clinicians did not have a role in delivering the trial interventions, they were informed about the trial and were provided with information about the trial for any clinicians or patients who needed it.

Hospitals were contacted initially to ascertain survival of patients handed over from ambulance services to the ED. If the patient had survived, the research paramedics liaised with the hospital clinicians to visit the patient and seek consent for continuation in the trial (see Consent).

For any patient taken to hospital, data were collected on survival, length of stay in hospital and ICU, targeted temperature management, adrenaline use and mRS score at discharge, as well as discharge address and GP details. As some patients were found in a public place without any identifiers, or only part of their details were known to the ambulance service at the time of arrest, hospitals also, when necessary, provided missing information such as name, address and date of birth.

Survival checks

Survival checks were completed by the ambulance service research teams or the WCTU trial team using a variety of sources:

• hospital data

• Summary Care Record/Welsh Demographic Service

• GP surgeries.

Follow-up

Survivors willing to take part were followed up approximately 3 months and 6 months after their cardiac arrest, as per Figure 4. Whenever possible, the 3-month assessments were a home visit, but, if the patient preferred postal questionnaires or to go through the questionnaires over the telephone, this was arranged, although the MMSE was not completed over the telephone. Questionnaires at the 6-month time point were sent by the WCTU and returned by post.

Following the approach to the patient, in the unlikely event that we had not obtained a response from the patient, the WCTU trial team approached the patient’s GP or hospital or ambulance service for information on their mRS score as close to the 3- and 6-month time points as possible. If the 3-month booklet had not been completed by the time the 6-month visit was due, the patient was sent the 3-month booklet to complete instead, so that outcomes that are only collected at 3 months were not missed.

Data linkage with other data sets

Data on each patient’s stay in hospital were collected retrospectively from the following electronic data sets to provide data on length of stay in hospital and hospital interventions:

• Intensive Care National Audit and Research Centre (ICNARC).

• Patient Episode Database for Wales (PEDW).

• Hospital Episode Statistics (HES).

• UK Transplant Registry (UKTR).

An application was made to receive data from the National Institute for Cardiovascular Outcomes Research data set. However, the application was not approved in time for data to be received in time for analysis.

Quality of cardiopulmonary resuscitation

Information on CPR quality is increasingly being viewed as an international reporting standard for cardiac arrest research.

The executive summary of the European Resuscitation Council Guidelines for Resuscitation 201088 identifies four critical components of high-quality CPR: minimise interruptions in chest compressions (as measured by chest compression fraction), provide compressions of adequate rate, provide compressions of adequate depth and allow full chest recoil between compressions.

Because a way to measure chest recoil was unavailable, the first three parameters were measured:

1. chest compression fraction, also known as chest compression ratio

2. chest compression rate

3. chest compression depth.

A preliminary review of existing literature showed that these three variables are typically studied using measurements covering two time periods:

1. initial 5 minutes of recorded CPR treatment

2. whole episode of recorded CPR treatment.

To measure these indicators of the quality of CPR for PARAMEDIC2 trial cases, data were downloaded from defibrillators, when possible. Three models of defibrillators were used across two ambulance services:

• London Ambulance Service –

  • LIFEPAK^® 15 monitor/defibrillator (Physio-Control, Inc., Redmond, WA, USA)

  • LIFEPAK^® 1000 defibrillator (Physio-Control, Inc.).

• North East Ambulance Service –

  • X Series^® monitor/defibrillator (ZOLL Medical Corporation, Chelmsford, MA, USA).

When it was not possible to download quality of CPR data using existing means, a CPR card was used as a substitute. These Conformité Européenne-marked CPR cards, supplied by Laerdal Medical (Stavanger, Norway), measured compression fraction, compression rate and depth. CPR cards were operated by being switched on and placed centrally on a patient’s chest. Chest compressions were then performed as usual. Quality of CPR data were recorded during the resuscitation attempt, but the card did not provide real-time feedback to the paramedics.

In total, 1000 CPR cards were distributed to South Central Ambulance Service, the Welsh Ambulance Service and the West Midlands Ambulance Service. Trial-trained paramedics were taught how to use the CPR cards. Trial sites used site-specific processes to return used CPR cards from paramedics to site research teams. Site research teams downloaded data from the returned used CPR cards and provided the quality of CPR data securely to the WCTU. Data from both the defibrillators and CPR cards were entered into the trial database for analysis.

Table 4 compares the feasibility of acquiring the needed parameters and measurement periods from the devices used for the PARAMEDIC2 trial. The X Series defibrillator records all three parameters; an arithmetic mean (or average) value is given for the whole treatment episode and arithmetic mean values are also given for 1-minute intervals. The CPR cards record all three parameters, with an arithmetic mean value given for the whole treatment episode only; 1-minute intervals are not possible. The LIFEPAK 15 and LIFEPAK 1000 defibrillators record compression rate and compression fraction only (compression depth is not possible without an additional puck-sized sensor). Instead of the arithmetic mean, a ‘trimmed mean’ value (namely a mean that removes the extreme observations) is given by the LIFEPAK defibrillators for the whole treatment episode, and also for each 1-minute interval.

Primary and secondary outcomes

The primary analysis was performed with and without adjustment in the modified intention-to-treat population, which included all the patients who had undergone randomisation and were confirmed to have received the assigned intervention.

Other approaches, for instance per protocol and complier-average causal effect, were not considered because of the negligible proportion of non-compliance. For data with a normal distribution, means and standard deviations (SDs) are presented. For data that were non-normally distributed, medians and IQRs are presented. Categorical data are summarised as frequency and percentage.

Fixed-effect regression models were used to examine survival outcomes with and without adjustment. Variables included in adjusted analyses were age, sex, the time between the 999 call and the ambulance arriving at the scene, the time between the ambulance arriving and trial drug administration, the suspected aetiology of the cardiac arrest, the initial heart rhythm, whether or not the event was witnessed and whether or not a bystander undertook CPR.

Length-of-stay outcomes were examined by the Hodges–Lehmann117 method, and were reported as estimated median differences with 95% CIs. When modelling the mRS, scores of 0–3 were classified as ‘good’ and scores of 4–6 were classified as ‘poor’; that is scores of 0–3 were regarded as a ‘good’ outcome and scores of 4–6 were regarded as a ‘poor’ outcome. If the proportional odds assumption was violated in modelling the mRS, partial proportional odds models118,119 were used. Other secondary outcomes (including quality of life and neurological and cognitive functions) were summarised by treatment arm.

Sensitivity

A sensitivity analysis was prespecified for mRS scores at discharge and at 3 and 6 months if > 10% of the data of survivors at each time point were missing. We used last observation carried forward and best- and worst-case scenarios for imputation. For the best-case scenario, missing data are considered as having no symptoms. For the worst-case scenario, missing data are considered as having severe disability in those confirmed to be alive at follow-up, and dead in those with confirmed death or missing survival status at follow-up. Post hoc sensitivity analyses were conducted for survival at 30 days, survival at hospital discharge, and survival with a good neurological outcome at discharge and at 3 and 6 months. Best-case and worst-case scenarios and multiple imputation were used.

Unadjusted and adjusted analyses were conducted for the primary and secondary outcomes, apart from the Two Simple Questions tool. Unadjusted and adjusted ORs with 95% CIs and mean differences with 95% CIs were reported for categorical and continuous outcomes, respectively. The number needed to treat and its 95% CI were calculated for survival at 30 days.

Quality of cardiopulmonary resuscitation

We used only the data on quality of CPR collected by London Ambulance Service because insufficient data were collected from the other sites. The Mann–Whitney U-test was used to compare treatment differences in hospital- and ICU-free survival because of their non-normal distributions.

Subgroups

Prespecified subgroup analyses included a patient’s age, cause of cardiac arrest, initial cardiac rhythm, whether or not the cardiac arrest was witnessed, whether or not CPR was performed by a bystander, interval between the emergency call and ambulance arrival at the scene, interval between ambulance arrival and the trial-agent administration, and the interval between the emergency call and trial-agent administration. A p-value for interaction was reported in each analysis.

Reporting of analyses followed CONSORT guidelines.

Interim analyses

Prior to the start of the trial, we used the Lan–DeMets,120 O’Brien–Fleming and Pocock alpha spending methods to determine the upper and lower stopping boundaries for the primary outcome, with no adjustment in the final analysis. Interim analyses were carried out 10 times on a quarterly basis during the trial recruitment. Reports were delivered confidentially to the DMC. The DMC reviewed these results and made recommendations to the TSC about continuation of recruitment or any modification to the trial that may have been necessary.

The DMC monitored the accumulating outcome data; one of its roles was to recommend cessation of recruitment if a clear result had been reached (i.e. if either adrenaline or placebo was clearly superior). We suggested that different thresholds of evidence for early termination were adopted if adrenaline or placebo was being more effective, as it was probable that stronger evidence would be needed to change current practice (adrenaline use) if adrenaline was found to be inferior. We therefore proposed that interim analyses were conducted frequently in the early stages of the trial, so that, if adrenaline was superior, this was detected earlier. Thus, we minimised any risks to patients while producing robust evidence that will change practice if adrenaline is inferior.

The outcomes of primary interest for the interim analyses were 30-day survival and neurological status. We prepared reports for the DMC initially every 3 months. The exact schedule of interim analyses and the nature of any early-stopping rules were determined by the DMC, in discussion with the investigators, before the start of recruitment.

Bayesian analysis

To aid in interpretation, we included a Bayesian analysis for the primary outcome and for survival with a favourable neurological outcome. The Bayesian statistical analyses were performed using RStan. All other statistical analyses were performed with the use of SAS^® software, version 9.4 (SAS Institute Inc., Cary, NC, USA).

We performed unadjusted Bayesian analyses for two outcomes, 30-day survival and survival with favourable neurological outcome, to enable us to quantify the probability of treatment effects of different sizes. We modelled the adrenaline and placebo arms separately, with the outcome for each participant being a Bernoulli (0/1) variable, with treatment arm-specific probabilities of ‘success’. Non-informative beta(1, 1) priors (Figure 7) were used for both groups, initially. We also performed a sensitivity analysis assuming more realistic, informative priors. These were beta(5, 150) for the adrenaline group (Figure 8), reflecting previous knowledge that survival in the adrenaline group was very unlikely to exceed 10%, and was most likely to be around 3%, and beta(2, 20) for the placebo group (Figure 9), because a survival rate exceeding 20% in the placebo group was very unlikely.

FIGURE 7.

Beta(1, 1).

FIGURE 8.

Beta(5, 150).

FIGURE 9.

Beta(2, 20).

We calculated the 95% and 80% highest-density intervals, and, for risk differences, the probability that the treatment effect exceeded 0%, 1% and 2% (which have been suggested as representing clinically important differences).

We present the results for the analyses of risk differences for both outcomes with the non-informative prior. The informative priors made only very minor differences to the results.

Economic evaluation

A within-trial economic evaluation and decision-analytic model that extrapolated economic outcomes beyond the trial-follow-up period were based on the trial design. The economic evaluation was conducted from the recommended NHS and PSS perspective. 121 Further details of the economic evaluation methods are presented in Chapter 4.

Quality control of protocol non-compliances

Protocol violations were monitored using statistical process control charts. The monthly number of violations and the proportion as a percentage of recruitment were plotted. The moving range, defined as the absolute value of month-to-month change, was plotted against the recruitment month. Any out-of-control conditions, defined as outside the prespecified limits, were investigated for quality control.

Conducting a placebo-controlled trial

As adrenaline is currently part of standard clinical treatment in cardiac arrest, a placebo controlled trial necessitates some patients not receiving standard treatment. To justify the use of a placebo in place of standard treatment, it was necessary to demonstrate that current evidence on the use of adrenaline in cardiac arrest raised sufficient doubt about its efficacy and concern about its potential harm to patients, to justify a trial that involved withholding adrenaline from some participants. There is an ethical obligation for health-care professionals to provide treatment that imparts the most benefit and least harm for the patient, based on the best available evidence. Our review of the available evidence concluded that adrenaline, as currently used, improves the rate of ROSC), but increases the likelihood of neurological damage in those patients who survive and leave hospital. Thus, adrenaline can cause benefit and harm, and it was not clear from available evidence whether or not it caused more harm than benefit.

Given the uncertainty of the evidence, and the potential life-threatening nature of the condition being treated, it is ethically important to obtain the best evidence we can to justify treatment, while ensuring that the interests of the research participants remain paramount. Based on available evidence, the risks and benefits from participating in the trial were reasonably balanced (if a participant was randomised to placebo, they may have a reduced chance of immediate survival, but an increased chance of surviving to leave hospital neurologically intact). Our initial patient and public involvement (PPI) work suggested that members of the public value long-term survival more than short-term recovery of spontaneous circulation, so it would seem reasonable to assume that potential participants might agree to take part in a placebo-controlled trial, if they were able to do so.

Using a model of deferred consent

Enrolment in a clinical trial of a medicinal product normally requires informed consent from the participant or, if the participant lacks capacity, their legal representative. A decision about participating in a trial with potentially life or death consequences is particularly challenging, and, when treatment is not urgently required, the consent process may take considerable time. The unpredictability and immediately incapacitating nature of cardiac arrest (sudden loss of consciousness) means that it is not possible to obtain prospective informed consent from participants. Because of the need for immediate treatment, it is also not possible to obtain consent from the patient’s legal representative. This situation is ethically challenging as it is not possible to respect the participant’s autonomy by enabling them to make an informed choice regarding participation. The ethical justification for over-riding the usual requirement for consent must therefore be substantial with regard to the potential for the research to provide future benefit to patients or to protect them from future harm. All clinical trials of IMPs in the UK are governed by the EU Clinical Trials Directive (2001/20/EC)122 and the Statutory Instrument 2004/1031 [The Medicines for Human Use (Clinical Trials) Regulations 2004]. 123 In designing and conducting this trial, we also complied with the 2006 amendment to these regulations, relating to emergency care research that permits enrolment without consent in the emergency situation, subject to approval by an appropriate REC, and with a requirement that consent is obtained once it is no longer necessary to take action as a matter of urgency (deferred consent). Our approach was based on the template outlined at the Health Research Authority Workshop 2012 on conducting emergency research in patients who lack capacity. 125

The ethics implications of the deferred consent model [referred to as ‘exception from informed consent’ (EFIC) in the USA] in relation to the constraints on the principle of respect for autonomy, and approaches to mitigate these, have been discussed in the academic literature. 126–130 Providing information to, or undertaking consultation with, the relevant population prior to the research taking place can assist in the assessment of whether or not the research is sufficiently important in terms of the clinical benefit to patients to warrant the use of deferred consent. In the initial stages of trial design, we consulted PPI members from the first PARAMEDIC trial, and held a community engagement event where the rationale of the trial was presented to 280 lay people with an interest in first aid (see Patient and public involvement).

Providing information prior to and during the trial also allows the opportunity for potential participants to register their wish not to participate, and for researchers to respect their autonomous prior refusal. In the USA, some RECs (Institutional Review Boards) require researchers in EFIC studies to provide a mechanism for potential participants to opt out. 131 In the UK, it is rare for trials in emergency care to provide this option. For the PARAMEDIC2 trial, we developed a substantial public communications policy and included a mechanism for members of the public to register their wish not to participate, which included provision of ‘opt-out’ bracelets to be worn during the trial period (see Procedure for taking consent).

Approaching patients or their relatives (or legal representative) to inform them about enrolment in the trial and to seek consent for continuation in the trial also required careful thought in balancing the importance of providing information as soon as possible following the emergency and minimising distress caused by approaching relatives of patients critically ill in intensive care. Many patients lacked capacity to consent to participation in the early stages of recovery and some patients regained capacity over the period of the trial. Our consent processes were responsive to these complexities within the legal framework of the European Directive122 (see Procedure for taking consent).

Informing families of patients who do not survive cardiac arrest

The sad reality of an OHCA is that fewer than 1 in 10 people survive. Experiencing the sudden unexpected loss of a loved one because of cardiac arrest is a traumatic event that frequently leads to symptoms of anxiety, depression and post-traumatic distress. Careful consideration therefore needed to be given to how, when and if the relatives of non-survivors were to be informed about participation in the trial. By the time a patient’s death occurred, the trial intervention would have been implemented and no further follow-up would occur. Thus, there would be no requirement to seek consent to continue, and nor would it be useful to do so. The purpose of any communication with the family/next of kin of the deceased would be to inform them about the patient’s involvement in the trial, demonstrating that the process of trial recruitment is open and transparent. In addition, it mitigates any potential harm to family members from discovering at a later date that their relative or friend had been involved in a trial without their knowledge. However, knowledge of trial participation after the event may also place a significant burden on the next of kin at a time of heightened emotional distress due to the loss of their relative or friend. Any strategy to inform the family or next of kin following a patient’s death needs to balance the need for transparency with the need to minimise this distress.

The research team, including the trial ethicist, considered this issue with great care and discussed different approaches with patient representatives, clinicians caring for patients who had experienced a cardiac arrest and their families, the Resuscitation Council, and the REC. Approaches to informing the relatives of participants who do not survive can be broadly categorised as passive or active. Passive methods include placing information about the trial in publicly accessible places (e.g. websites, newsletters) and targeted sites likely to be attended by relatives of the deceased (e.g. hospitals, general practice surgeries, Registrar of Births and Deaths offices), with a contact telephone number and address for further information. This approach allows people to make a choice about whether or not and when they wish to seek further information. However, it is uncertain whether or not relatives of participants will see them. Discussion with investigators of previous UK trials in emergency of life-threatening conditions suggested that passive strategies, although not formally evaluated, had been used successfully.

Active strategies involve making direct contact with relatives through a face-to-face meeting, a telephone call or written communication. To our knowledge, this approach has not been used in previous UK OHCA trials, so we were unable to draw on relatives’ or researchers’ experiences of this process. There are practical barriers to providing information actively. The sudden and unpredicted nature of cardiac arrest mean that the relatives/next of kin are neither universally present nor identifiable at the time of the cardiac arrest. Information on the identity of the relatives/next of kin are also not held by ambulance services, so follow-up at a later date or time may not be possible. For people for whom resuscitation efforts are terminated in the home (≈ 40% of total cases), it is not possible for the attending paramedic to spend the necessary time to explain about the trial, answer questions and provide support to relatives who will be extremely distressed. Alternatively, providing unsolicited written information by post could exacerbate an already traumatic and stressful experience.

Having assessed the balance of benefits and burdens for relatives of the different strategies, and taking into account the importance of transparency, we concluded that the burden to families of adopting an active information strategy outweighed the potential benefits. We therefore developed a passive information strategy with a clear process for responding to enquiries from relatives of participants (and the general public) (see Procedure for taking consent and Enquiries regarding trial participation).

Subgroup analysis

The treatment effect on survival to 30 days was further assessed in the prespecified subgroups. Survival rate was consistently higher in the adrenaline arm, but the results indicated no evidence of significant treatment difference across subgroups in both unadjusted (Figure 18) and adjusted analyses (Figures 19) (interaction p > 0.05).

FIGURE 18.

Unadjusted subgroup analysis.

FIGURE 19.

Adjusted subgroup analysis.

Data linkage

Patients who survived on the scene and were transported to hospital were included for data linkage (Figure 20). Data linkage to HES, the PEDW, the ICNARC data set and the UKTR was conducted for the health economic analysis. The overall match rate of the ICNARC data set and the UKTR are 22.9% and 5.5%, respectively.

FIGURE 20.

Data linkage to UKTR and ICNARC.

The linkage rates for the HES data sets are 96.4% for the PEWD (Welsh HES), 82.1% for NHS Digital and 92.2% across both data sets.

Serious adverse events

No events fulfilling the criteria for SAEs, SARs or SUSARs were reported during the trial.

Protocol deviations and violations

Table 13 shows the type and frequency of protocol deviations and violations throughout the trial, and Figure 21 shows the number of violations over time as a proportion of recruitment in each month. Overall, the proportions were small. The peak in October 2015 was mainly as a result of the small number of participants recruited by this early stage. The dotted line shows the decreasing trend of violations over time. Figure 22 is the statistical process control chart of the change of protocol violations over time, as a percentage of recruitment, from June 2015 to October 2017. The violation had large variation at the early stage, due to the peak in October 2015 (see Figure 22). The change then stabilised and was mostly limited to the upper one-sigma (SD) limit.

FIGURE 21.

Frequency of protocol violations over time.

FIGURE 22.

Statistical process control chart of the frequency of protocol violations over time as a percentage of recruitment.

Serious breaches

Two serious breaches occurred during the trial, as outlined in the following sections.

Assessment of impact of protocol non-compliances

It is the assessment of the TMG that the trial complied with GCP and that the deviations, violations and serious breaches did not have any material impact on the trial findings.

Initial emergency response

Resource inputs associated with the initial pre-hospital emergency response were extracted from the trial CRFs completed by research paramedics. These data included the number of emergency response staff/ambulance crew and vehicles in attendance, the duration of the emergency response and the cumulative adrenaline doses administered. Emergency response duration was defined as (1) the interval between the at-scene time (i.e. the time at which the emergency response team arrived at scene) and the left-scene time (or the time at which CPR was stopped if the left-scene time was not recorded) if the cardiac arrest occurred at home and the patient was pronounced dead at scene, or (2) the interval between at-scene time and arrival-at-hospital time if the patient survived and was taken to hospital.

It was assumed that one vehicle transported the patient to hospital if multiple vehicles were in attendance, with the remaining vehicles standing down and available for the next assignment. Consequently, a 1-hour stand-down time was added to the emergency response time for each patient to account for ambulance crew stand-down and restock time following discussions with the trial paramedics about duration of these activities under current UK clinical practice. Sensitivity analyses (see Table 14, sensitivity analyses 11 and 13) explored the impact of excluding the cost of emergency response crew stand-down and restock time on cost-effectiveness outcomes.

Initial emergency response data were generally collected for trial participants up to the point of death or hospital admission. This meant that trial data were not available to estimate some resource inputs for patients who died at scene. In particular, the trial CRFs did not record post-death ambulance crew activity, such as whether or not the deceased person was transported to a mortuary. Thus, it was assumed that patients pronounced dead at the scene of the cardiac arrest would be left at the scene if the location of the cardiac arrest was the patient’s home, and would be transported by emergency ambulance to the nearest hospital or public mortuary if the location of the cardiac arrest was a public place. Google Maps (Google Inc., Mountain View, CA, USA) [called from within R (The R Foundation for Statistical Computing, Vienna, Austria) via packages ‘gmapsdistance’ and ‘googleway’] was then used to estimate ambulance travel time to the nearest hospital mortuary for the subgroup of patients whose arrest occurred in a public place. Sensitivity analyses explored the impact of variations in this assumption on the base-case cost-effectiveness results (see Table 14, sensitivity analyses 12 and 13).

Hospital- and community-based health and social care service use

Data on the use of hospital- and community-based health and social care services covering the 6-month period from randomisation were collected for trial participants by three principal means:

1. Trial CRFs completed by research paramedics provided details of the initial hospitalisation episode, including ED assessment and treatment and inpatient length of stay in the ICU and cardiac and general adult wards.

2. Hospital Episode Statistics134 were requested for trial participants, covering the period from each participant’s cardiac arrest event to 31 March 2018. This provided a complete profile of resource use associated with all hospital episodes for all participants over the trial time horizon, including ED attendances, outpatient attendances, day-case admissions and critical care and other inpatient admissions covering procedures undertaken and lengths of stay. When HES data were not available, data collected using the trial CRFs and patient self-reports of hospital-based service use were used instead.

3. Economic questionnaires completed by trial participants or their proxies at the 3- and 6-month post-randomisation assessment points provided details of hospital re-admissions and use of hospital outpatient services, community health and social care services, prescribed medications, NHS supplies, child-care costs, time off work and out-of-pocket medical expenses.

Valuation of hospital resource use collected through trial case report forms

Hospital resource inputs were estimated for trial participants using the trial CRFs and valued by attaching unit costs drawn largely from secondary sources. Hospital-based services included inpatient admissions, outpatient visits and diagnostic tests and scans. Unit costs for these services were obtained primarily from the 2016/17 NHS reference costs main schedules,135 and acted as an alternative source of hospital cost values to the HES-generated data. Average daily unit costs were calculated for hospital-based services using a costing methodology previously described in a HTA report that informed an economic evaluation of a mechanical versus manual CPR for OHCA. 136 The costing method involves assigning identifying Healthcare Resource Group (HRG) codes for clinical care most likely to be received following OHCA and calculating a per diem cost weighted by the level of activity.

Valuation of Hospital Episode Statistics data

The HRG4+ 2016/17 Reference Costs Grouper137 was used to generate HRG codes for each record of admitted care and critical care episode, ED attendance, and outpatient visit extracted from HES for each trial participant. Records were matched to grouper costs in the 2016/17 NHS Reference Costs main schedules135 based on the HRG and combination variables describing the level of resource use associated with each episode of care. ED and outpatient attendances were matched to averaged reference costs based on the HRG code only. Admitted care episodes were matched at the full consultant episode level based on the HRG, patient classification (admitted vs. day case), type of admission (elective vs. non-elective) and length of stay (short stay vs. long stay). Inpatient length of stay was defined as short stay if the episode duration was 1 day and was described as long stay for episodes lasting ≥ 2 days, in line with national reference cost calculations (see pages 47 and 48 of the National Cost Collection guidance 2018138).

Unbundled HRGs associated with high-cost drugs, devices and investigations and excess bed-days were automatically generated by the Grouper software for each admitted care record. Reference costs were attached to unbundled HRGs and excess bed-day costs generated by multiplying the duration of excess bed-days by respective excess bed-day unit costs in the 2016/17 reference cost schedules. 135 Costs were summed across full consultant episodes within spells to generate total costs per admitted care spell covering the total time period between admission and hospital discharge. Critical care records were matched to reference costs based on the critical care HRG, and critical care unit function code describing type of critical care activity. Non-specific general adult critical care patients and the maximum number of organ systems supported at any one time during the critical care period predominate in the algorithms were used to cost critical care episodes. 139

Resource use and economic costs extracted from participant-completed questionnaires

Economic questionnaires completed by trial participants or their proxies at the 3- and 6-month post-randomisation assessment points provided resource use data that complemented the resource use data extracted from the trial CRFs and HES data sets. Details of hospital re-admissions, by type and duration of hospital admission and hospital outpatient service, by type and volume, were extracted from the economic questionnaires and valued using 2016/17 NHS reference costs main schedules. 135

Primary and community health and social care services included face-to-face or telephone contacts and/or home visits by a general practice doctor, practice nurse, community physiotherapist or other community health or social care professionals. Consultation costs were derived from the Personal Social Services Research Unit’s Unit Costs of Health and Social Care 2017. 140 The cost of prescribed medication was obtained primarily from the prescription cost analysis 2017 database141 and electronic searches of the British National Formulary (BNF) 2017 edition. 142 Typical dosages and durations of treatment reported in the BNF for each medication were used in calculating quantities of individual preparations if the daily dose and/or duration of a course of medication was not reported in the trial documentation.

The quantities of over-the-counter medicines were rounded to the nearest pack and unit costs were obtained from online sources. Costs of aids and supplies (e.g. walking aids, heart monitors) were either provided by the trial participants themselves (if self-purchased) or derived from the NHS supply chain catalogue for aids and supplies provided by health providers during the trial follow-up period. Unit costs for health-care resource inputs were inflated/deflated to 2016/17 prices when necessary using the NHS Hospital and Community Health Services Pay and Prices Index, and the Consumer Prices Index. 140

The economic questionnaires completed by trial participants or their proxies at the 3- and 6-month post-randomisation assessment points also provided details of broader societal (non-NHS/PSS) resource input and costs, such as out-of-pocket medical expenses (e.g. privately purchased medication, travel costs as a result of hospital and medical appointments), child-care costs, income lost, housework help and laundry services costs. Out-of-pocket medical expenditure (e.g. medication purchased by patients themselves and travel costs) were either provided in monetary terms or valued by attaching unit costs to resource inputs provided. Non-health-care costs such as child-care costs and lost income were generally provided by participants and/or their proxies in monetary terms; therefore, no requirement to value these outcomes was necessary.

Estimation of costs for the total 1-year period after randomisation

Hospital Episode Statistics134 were requested for trial participants covering the period from the cardiac arrest event to 31 March 2018. This meant that patients followed up after this date had incomplete HES records covering the 1-year period after the cardiac arrest event. The following methodology was used to calculate 1-year hospital costs estimates for all inpatients, including those with < 1 year of complete HES data:

• Hospital Episode Statistics data were available for 1833 (45.7%) participants in the adrenaline group and 1094 (27.4%) participants in the placebo group. Of these, complete records of hospital resource use up to 1 year were available for 1802 (98.3%) of the 1833 in the adrenaline group and 1068 (97.6%) of the 1094 in the placebo group. These data were used to estimate costs of hospital care (initial hospitalisation episode, re-admissions and use of non-admitted hospital care services such as day-case admissions, ED attendances and outpatient attendances) covering the period between the cardiac arrest event to 1 year post event. The remaining 31 (1.7%) patients in the adrenaline group and 26 (2.4%) in the placebo group had HES-based records of hospital resource use for < 1 year. The 1-year costs of hospital resource use for these patients were treated as missing data.

• Of the remaining 2182 (54.3%) trial participants in the adrenaline group and 2905 (72.6%) trial participants in the placebo group who did not have HES data, 1984 (90.9%) in the adrenaline group and 2778 (95.6%) in the placebo group died at the scene of the cardiac arrest or were not taken to hospital. We assigned zero hospitalisation costs to these patients. The remaining 198 (8.1%) and 127 (4.4%) participants in the adrenaline and placebo groups, respectively, who were taken to hospital but had no HES records were either treated as missing data (if they declined consent to continued participation) or assigned 1-year hospitalisation costs based on the CRFs and data collected through the economic questionnaires completed by trial participants or their proxies.

• The cost of hospital resource use covering the 0–6 months post-randomisation period was estimated based on resource use extracted from the CRF and economic questionnaire data. The costs of hospital re-admissions and non-admitted care services in the 6- to 12-month window were estimated by extrapolating costs incurred in the 3- to 6-month period to 6–12 months. This essentially multiplied the 3- to 6-month costs by three for the calculation of 1-year hospital costs.

• Finally, 1-year costs associated with the use of non-hospital-based health and social care services and societal costs were estimated by extrapolating costs incurred at 3–6 months post randomisation (derived from participant-completed questionnaires) to 6–12 months post randomisation for all trial participants.

Health-related quality of life and survival

Health-related quality of life was assessed using generic instruments (i.e. the EQ-5D-5L and SF-12 version 2) completed at 3 and 6 months post randomisation and the mRS instrument completed at hospital discharge and at 3 and 6 months post randomisation. Responses to the EQ-5D-5L descriptive system were converted into health utility (or preference-based health-related quality-of-life) values, based on the UK EuroQol-5 Dimensions, three-level version (EQ-5D-3L), tariff143 using the van Hout et al. 144 interim cross-walk algorithm, in line with current NICE recommendations. 145 The mRS scores were converted into health utility (or preference-based health-related quality-of-life) values, based on the UK EQ-5D-3L tariff,143 using a published mapping function developed by Rivero-Arias et al. 146 The SF-12 scores were converted into health utility values using the Short Form questionnaire-6 Dimensions (SF-6D) utility tariff for the UK published by Brazier et al. 147 Survival outcomes following cardiac arrest were also collected to 12 months post cardiac arrest for trial participants.

Quality-adjusted life-years

Quality-adjusted life-year profiles were generated for each trial participant using area-under-the-curve methods, assuming a baseline health utility value of zero and linear interpolation between utility measurements, taking into account survival over the 6-month time horizon of interest (base case). In the base-case analysis, we combined utility values from the mRS scores at hospital discharge and utility values derived from the EQ-5D-5L at 3 and 6 months to calculate QALY profiles over 6 months. We used mRS-derived health utilities in place of EQ-5D-5L values if the latter were missing at the 3- or 6-month post-randomisation assessment points. 146 Health utility values generated from the mRS were available at hospital discharge and at all assessment points over the 6-month base-case time horizon. Thus, the impact of combined EQ-5D-5L-/mRS-generated QALYs on the base-case cost-effectiveness results was assessed in a sensitivity analysis that used QALYs generated solely from the mRS scores. Patients who died were assigned a utility value of zero onwards from time of death for the calculation of QALYs.

We did not assess health-related quality of life at baseline, as the clinical context precluded collecting any patient-reported outcome data around the time of randomisation: patients were either unconscious or too critically ill to complete questionnaires. 148 Alternative assumptions around health-related quality of life at baseline explored the impact on the cost-effectiveness of adrenaline of setting the baseline utility value to zero. In the first of these, the baseline utility value in the adrenaline and placebo groups was set to –0.402, reflecting UK population preferences for an unconscious health state within the EQ-5D-3L A1 tariff set. 149

We also calculated QALY profiles over 12 months, under the assumption that patients’ health-related quality of life at 12 months was the same as their health-related quality of life at 6 months, if they had survived, and we used this information to inform a sensitivity analysis exploring longer-term cost-effectiveness.

Summary of resource use and costs

Patient-level costs were generated for each resource variable by multiplying the quantity reported by the respective unit cost, weighted by length of stay or duration of contact when appropriate. Summary statistics (means, standard errors and completion rates) were generated for the whole trial population and for those surviving to hospital discharge by treatment allocation and assessment point. Between-group differences in mean resource use and mean costs at each assessment point were compared using the two-sample t-test. Statistical significance was assessed at the 5% significance level. A non-parametric bootstrap routine was implemented, generating 1000 replications of the data. Estimates of standard errors surrounding mean resource use (or cost) estimates and 95% CIs surrounding between-group differences in mean resource use (or costs) were obtained from the bootstrapped samples.

Summary of health-related quality-of-life data

Responses to each health dimension of the EQ-5D-5L and SF-12 are presented by level of function. Comparisons of responses were conducted on the basis of optimal level of function (e.g. ‘no problem’ on the EQ-5D-5L) versus suboptimal level of function (indicating any functional impairment). Between-group differences in optimal versus suboptimal level of function for each health dimension were compared for each outcome measure using chi-squared (χ²) tests at each assessment point for each health-related quality-of-life instrument. Summary statistics (means, standard errors and completeness rates) for health utilities were generated for the whole trial population and for survivors to hospital discharge by treatment allocation, assessment point and health-related quality-of-life instrument. Estimates of between-group difference in mean health utility values and 95% bootstrapped CIs surrounding mean group differences were generated based on 1000 bootstrapped resamples of the data.

Missing data

In addition to trial-specific protocols and procedures to minimise missing data, a strategy was employed prior to commencement of recruitment to identify and collect resource use and health outcomes data from multiple sources, with the specific aim of reducing the level of missingness for the economic outcomes of interest. Participants were assumed to incur no health-care costs beyond the initial emergency response costs if cardiac arrest occurred at home and the patient was declared deceased at the scene of arrest. Costs associated with use of hospital-based services were generated primarily from HES data; information obtained through trial-specific procedures (trial CRFs and participant questionnaires) was used when HES data were not available.

Health-related quality of life was assessed using multiple instruments, including the mRS completed at hospital discharge and the mRS, EQ-5D-5L and SF-12 completed by trial participants at 3 and 6 months post randomisation. Survival information was collected through trial-specific procedures and Office for National Statistics data. This process of using multiple data sources to systematically fill in missing data provided a more complete profile of the main economic outcomes of interest, compared with relying on a single data source.

Nevertheless, multiple imputation by chained equations (MICE), implemented through the R package MICE,150 was used to predict values for any remaining missing items, assuming data were missing at random. Missing costs and health utility values were imputed at the level of resource category and health-related quality-of-life assessment, stratified by survival status at hospital discharge and treatment allocation in accordance with good-practice recommendations outlined in Faria et al. 151 Imputation was achieved using predictive mean matching, which has the advantage of preserving non-linear relationships and correlations between variables within the data. Twenty imputed data sets were generated and used to inform the base-case and subsequent sensitivity and subgroup analyses. Parameter estimates were pooled across the 20 imputed data sets using Rubin’s rules to account for between- and within-imputation components of variance terms associated with parameter estimates.

Base-case cost-effectiveness

The base-case cost-effectiveness analysis used the intention-to-treat data to estimate the cost–utility of adrenaline, compared with placebo, from the perspective of the UK NHS and PSS. 132 Economic costs and QALYs were calculated for each patient over a 6-month post-randomisation time horizon. Total costs were calculated by summing costs associated with the initial emergency response (including the cost of the intervention) and costs of broader hospital- and community-based health and social care services. QALYs were generated based on health utility data generated from the mRS score at hospital discharge and the EQ-5D-5L score at the 3- and 6-month assessments.

Two seemingly unrelated normal error regressions were fitted to imputed data using the systems fit implementation in R,152 which accounts for the correlation between patient-level costs and QALYs. The regressions controlled for treatment allocation, age, sex, time to first dose administration, cause of cardiac arrest, whether or not the cardiac arrest was witnessed, bystander CPR and rhythm. The base-case analyses were replicated using the Stata^® version 15 (StataCorp LP, College Station, TX, USA) MICE and seemingly unrelated regressions SUR REG functions.

The incremental cost-effectiveness ratio (ICER) was calculated for adrenaline, compared with placebo, by dividing the between-group difference in adjusted mean total costs by the between-group difference in adjusted mean QALYs. Cost-effectiveness was assessed by comparing the ICER to cost-effectiveness thresholds of between £15,000 and £30,000 per QALY gained, in line with NICE guidance132 and the recent empirical threshold of £13,000 per QALY estimate suggested by Claxton et al. 153 Estimates were also generated assuming £50,000 and £100,000 values for the cost-effectiveness threshold for a QALY, reflecting potentially higher willingness-to-pay thresholds for a life-saving intervention. The incremental net (monetary) benefit of adrenaline compared with placebo was calculated for cost-effectiveness thresholds ranging from £15,000 to £200,000 per QALY gained. Net monetary benefit values reflect the opportunity cost of (or the benefits forgone from) adopting a new treatment when resources could be put to use elsewhere. A positive net monetary benefit suggests that, on average, adrenaline provides a net gain, compared with placebo, for the health service and can be considered cost-effective at the given cost-effectiveness threshold.

Uncertainty around the mean cost-effectiveness estimates was characterised through a Monte Carlo method. 154 This involved simulating 1000 replicates of the ICER from a joint distribution of the incremental costs and QALYs and plotting the simulated ICERs on the cost-effectiveness plane. A sensitivity analysis explored an alternative characterisation of uncertainty based on generating 1000 bootstrap replications of the ICER instead of the Monte Carlo method (see Table 14, sensitivity analysis 4). Cost-effectiveness acceptability curves (CEACs) were also plotted to give graphical display of the probability that adrenaline is cost-effective across a wide range of cost-effectiveness thresholds. A sensitivity analysis explored the impact of embedding the imputation model within the non-parametric bootstrap to simulate 1000 replicates of the ICER to calculate the probability that adrenaline is cost-effective at the cost-effectiveness thresholds specified previously.

Analysis of secondary health economic outcomes

Secondary health economic outcomes were analysed using logistic regression models that were embedded in the bootstrap and imputation models. The regression models estimated adjusted overall survival and neurologically intact survival probabilities for adrenaline and placebo at 6 months post randomisation. This preserved the correlation between patient-level costs and effects and allowed us to express the cost-effectiveness of adrenaline as incremental costs per unit increase in the proportion of patients surviving to 6 months post cardiac arrest.

Sensitivity analyses

Table 14 summarises methods and assumptions underlying the base-case and the sensitivity analyses conducted to explore the impact of alternative modelling assumptions and methods on the cost-effectiveness of adrenaline.

Subgroup analysis

Prespecified subgroup analyses were also conducted based on specifications in the PaRAMeDIC trial81 statistical analysis plan to explore whether or not there are subgroups of patients for whom adrenaline is likely to be cost-effective. In addition, one post hoc subgroup explored the treatment dose–response relationship and estimated the dose at which adrenaline is likely to be most cost-effective. Our subgroup analyses were as follows:

• Cardiac arrest witnessed by paramedic versus cardiac arrest witnessed by bystander versus cardiac arrest not witnessed.

• Bystander CPR versus no bystander CPR for bystander-witnessed and not-witnessed OHCAs.

• Type of initial rhythm: shockable (VT/VF) versus non-shockable (PEA/asystole).

• Aetiology of cardiac arrest (medical vs. non-medical).

• Age (≤ 60 years vs. > 60 years).

• Time interval from 999 call to EMS arrival (≤ 10 minutes vs. > 10 minutes) among those with a witnessed arrest.

• Time interval from EMS arrival to administration of trial drug (≤ 10 minutes vs. > 10 minutes) among those with a witnessed arrest.

• Time interval from 999 call to administration of trial drug (≤ 10 minutes vs. > 10 minutes) among those with a witnessed arrest.

• The time to emergency treatment variables were categorised based on previous studies reporting that administration of adrenaline within 10 minutes following cardiac arrest is associated with neurologically improved survival outcomes. 155

Extrapolating beyond trial follow-up

A simple Markov state-transition model was built in R using the package heemod156 to extrapolate the within-trial results over the lifetimes of cardiac arrest survivors. The model as shown in Figure 23 comprises four health states (OHCA state, post-OHCA survival with good neurological function, post-OHCA survival with poor/impaired neurological function and death). The cycle length is 1 year and all individuals start in the OHCA state at the incidence of cardiac arrest event. Possible transitions from this state represent 1-year survival with good or poor neurological function and death. This implies that the OHCA state captures all the economic costs and benefits in the first year after randomisation and so corresponds to the within-trial cost-effectiveness analysis with a 1-year time horizon. In the PARAMEDIC2 trial, neurological function was assessed at hospital discharge and at 3 and 6 months post randomisation. This information was used to categorise post-OHCA survival as good if the score of the mRS assessment closest to the 1-year time point after the cardiac arrest was ≤ 3 and to categorise it as poor for scores of > 3. Probabilities governing these transitions were estimated separately for the adrenaline and placebo groups, based on these categorisations, and are summarised in Table 15.

FIGURE 23.

Model to extrapolate cost-effectiveness beyond the PARAMEDIC2 trial follow-up. C, complement (probability of remaining in good or poor neurological functional states); good, good neurological function; poor, poor neurological function; pGood2Dead, annual probability of death among survivors with good neurological function; pPoor2Dead, annual probability of death among survivors with poor neurological function; pOHCA2Dead, probability of death within first year post cardiac arrest/from randomisation; pOHCA2Good, probability of surviving to 1 year with good neurological function; pOHCA2Poor, probability of surviving to 1 year with poor neurological function.

Possible transitions beyond the first year after the cardiac arrest event were restricted to movement from the good and poor functional states to death. The probabilities governing these movements were assumed to be independent of treatment allocation and were estimated from two sources. First, we estimated the conditional probability of surviving to 12 months, given that an individual had survived the first 9 months with good or poor function, and converted these estimates to 1-year probabilities using standard formulae. 158 Second, we obtained age- and sex-adjusted UK mortality statistics,157 assuming a starting age of 60 years and 78% probability of being male, reflecting the average cohort characteristics of survivors at 1 year post randomisation. We used this information to extrapolate survival beyond the first year post cardiac arrest to a lifetime horizon by assigning individuals a probability of death equivalent to the larger of the two estimates.

We assumed that patients surviving beyond the first year after the cardiac arrest event either died or remained alive in the same functional state at each modelled cycle (functional status cannot improve or deteriorate after first year post cardiac arrest). The assumption that neurological function cannot improve or deteriorate after the first year post cardiac arrest was made because of a lack of robust data to estimate the between-state transitions, and is consistent with recent economic models evaluating the cost-effectiveness of intervention in cardiac arrest. 159

Patients in the OHCA state were assigned cost and utility values obtained from the within-trial sensitivity analysis in which the time horizon was extended to 1 year. This covered the full spectrum of costs and QALYs incurred in the first year after the cardiac arrest event, adjusted for demographic and clinical characteristics. Costs associated with the good and poor functional states were estimated from resource use estimates covering the 3- to 6-month post-randomisation period collected for trial participants. Utility values associated with good and poor functional states were collected through the EQ-5D-5L reported by trial participants and stratified by functional status at the 6-month assessment point (see Table 15). Costs generated from resource use covering the 3- to 6-month period after randomisation were converted to 1-year costs assuming that the rate of resource use in this 3-month window is maintained over a period of 1 year. Costs and utilities were discounted at 3.5% per annum over the lifetime of cardiac arrest survivors.

Base-case analysis

The incremental cost-effectiveness of adrenaline is shown in Table 24 for the participants with costs and health outcomes data subject to multiple imputation. When an NHS and PSS perspective was adopted (i.e. that adopted for the baseline analysis), and health outcomes were measured in terms of QALYs based on the EQ-5D and mRS measures, the adjusted mean total cost was £3591 for the adrenaline arm, and £2285 for the placebo arm, generating a mean incremental cost of £1306 (95% CI £837 to £1774) over the first 6-month post-randomisation period. The adjusted mean QALYs was 0.0025 in the adrenaline arm and 0.0017 in the placebo arm, generating a mean difference in QALYs of 0.0008 (95% CI –0.0014 to 0.003). The ICER was £1,693,003. The probability that adrenaline was cost-effective at a cost-effectiveness threshold of £30,000 per QALY gained was zero. Extending the within-trial analysis to cover the 1-year period from randomisation by extrapolating costs and utilities measured at 6 months to 12 months reduced the base-case ICER from £1,693,003 per QALY gained to £644,308 per QALY gained for adrenaline, compared with placebo (mean incremental costs of £1411 and mean incremental QALYs of 0.0022). Extrapolating the within-trial analysis to cover the lifetime of survivors (see the model described in Chapter 4, Extrapolating beyond trial follow-up) reduced the ICER further to £81,070 per QALY gained (mean incremental costs of £1775 and mean incremental QALYs of 0.022).

Incremental net monetary benefits

The associated adjusted mean incremental net monetary benefits (INMBs) of adrenaline at cost-effectiveness thresholds of £30,000 per QALY were as follows: –£1282 for the within-trial base-case analysis (adjusted multiple imputation), 6 months post cardiac arrest event; –£1346 for extrapolation to 12 months post cardiac arrest event; and –£1118 for extrapolation to a lifetime time horizon (decision-analytic model) (see Table 24). The base-case mean INMB was < £0, suggesting that adopting the adrenaline protocol would result in a net economic loss of £1258, on average, from an NHS and PSS perspective [INMB –£1250 (95% CI –£1686 to –£815) at 6 months and –£1118 (95% CI –£2776 to £487) over the lifetime of survivors, assuming a cost-effectiveness threshold of £30,000 per QALY]. The CEAC shows that this results in a probability of cost-effectiveness of < 1% at cost-effectiveness thresholds of < £200,000 (see Appendix 1, Figure 25); that is, if decision-makers are willing to pay £30,000 for an additional QALY, the probability that adrenaline is cost-effective remains < 1% over the 6-month base-case within-trial time horizon and 11% over a lifetime time horizon (see Table 24).

Sensitivity analysis

Several sensitivity analyses were undertaken to assess the impact of uncertainty surrounding key parameters or methodological features on the cost-effectiveness results. The base-case analyses were replicated using Stata software and the results were consistent with the primary analyses. The adjusted and unadjusted complete-case analyses also exhibit the same pattern of results as the base-case analyses (see Appendix 1, Table 39). The probability that adrenaline is cost-effective remained relatively static (at about 0%) for the majority of the sensitivity analyses (i.e. societal costs, QALYs based on the mRS, 12-month time horizon, 12-month time horizon and societal perspective, and 12-month time horizon and QALYs based on the mRS). All sensitivity analyses showed that the average INMB value always remains < £0 (see Appendix 1, Table 39).

In sensitivity analyses that explored the impact of the missing not at random assumption on the within-trial base-case results, imputed utility values and costs were systematically decreased and increased while holding imputed values for other variables constant. The results are displayed in Appendix 1, Tables 40 and 41. They suggest that doubling the value of imputed utilities favoured adrenaline (the ICER decreased to £1,021,684 per QALY), whereas halving them favoured placebo (the ICER increased to £2,067,739 per QALY gained). Similarly, doubling imputed costs favoured adrenaline and decreased the ICER to £1,186,037 per QALY, whereas halving them had little effect on the within-trial base-case cost-effectiveness results (£1,688,008 per QALY). The probability that adrenaline is cost-effective was zero at cost-per-QALY thresholds of < £100,000 across alternative assessments, in which missing values for the main economic costs and outcomes were not assumed to be missing at random (see Appendix 1, Figures 28 and 29).

Subgroup analyses

To explore the heterogeneity in the cost-effectiveness results, 10 variables were considered: cause of cardiac arrest (medical, non-medical), age (≤ 60 years, > 60 years), sex (female, male), time from EMS arrival at scene to administration of first dose (≤ 10 minutes, > 10 minutes), time from 999 call received to EMS arrival at scene (≤ 10 minutes, > 10 minutes), shockable rhythm (yes, no), number of syringes given out of two (≤ 2, > 2), number of syringes given out of four (≤ 4, > 4), witnessed by (not witnessed, EMS, bystander), and bystander CPR (no, yes, unknown). All subgroup analyses were based on the patient-reported EQ-5D and mRS measures and used multiple imputation and covariate adjustments, as per the primary analyses (see Appendix 1, Table 42). Subgroups for which the probability of cost-effectiveness was > 10% at £30,000 per QALY gained over the 6 months within-trial time horizon were cardiac arrest of medical aetiology (probability of cost-effectiveness 15%), EMS witnessed (15%), aged > 60 years (20%), two or more doses of adrenaline administered (27%) and four or more doses of adrenaline administered (32%). All other subgroups generated probabilities of cost-effectiveness for adrenaline of < 10% at a cost-effectiveness threshold of £30,000 per QALY gained.

Secondary health economic outcomes

Results are presented in Table 25 for the cost-effectiveness of adrenaline expressed as incremental cost per unit increase in the proportion surviving to 6 months post cardiac arrest and the proportion surviving with good neurological function (i.e. neurologically intact survivor). The adjusted mean cost over 6 months was £3654 in the adrenaline arm and £2284 in the placebo arm, generating a cost-difference of £1370 (95% bootstrapped CI £954 to £1840). The 6-month adjusted survival probability was 0.0051 in the adrenaline arm and 0.0037 in the placebo arm, generating a difference in survival probability of 0.0014 (95% CI –0.0003 to 0.003) in favour of adrenaline. The 6-month adjusted probability of survival with good functional outcome was 0.0026 for adrenaline and 0.0023 for placebo, generating a difference in probability of 0.0014 (95% CI –0.0003 to 0.003) in favour of adrenaline. The ICER was £982,880 per percentage point increase in overall survival and £3,772,322 per percentage point increase in neurological survival.

Clinical outcomes

The use of adrenaline, in comparison with placebo, resulted in almost four times the number of patients being admitted to hospital after OHCA. This finding is broadly consistent with the findings of the PACA trial,56 which documented an OR of 3.4 (95% CI 2.0 to 5.6) for ROSC in favour of adrenaline over placebo for OHCA.

Many more patients in the adrenaline group than in the placebo group were admitted to hospital but did not survive to discharge: 2016 (50.2%) and 1209 (30.2%) patients in the adrenaline and placebo arms, respectively, were admitted, and 128 (3.2%) and 91 (2.3%) patients in the adrenaline and placebo arms, respectively, survived to discharge. Thus, 1888 patients in the adrenaline arm died in hospital, compared with 1118 in the placebo arm. We do not have data on the mode of death, but the majority of deaths occurred in the ED. These early deaths are more likely to be caused by circulatory failure or limitation of treatment due to the presence of severe comorbidities and functional impairment, as withdrawal of life-sustaining therapy resulting from perceived severe neurological injury should not normally occur until after 72 hours. However, although several studies have documented the mode of death among post-cardiac arrest patients admitted to an intensive trauma unit,161–163 this has not been well documented for those dying in the ED.

In the adrenaline group, 414 of the 566 (73.1%) patients admitted to the ICU died there, compared with 176 of the 270 (65.1%) placebo group patients admitted to the ICU. Thus, 238 additional patients in the adrenaline group were admitted to an ICU, but died there. Surviving patients spent, on average, 7 days in intensive care and 21 days in hospital. By the time of hospital discharge, 128 (3.2%) patients were alive in the adrenaline group, compared with 91 (2.3%) in the placebo group, of whom 87 (2.2%) and 74 (1.9%), respectively, survived with a favourable neurological outcome. Although, at the time of discharge, 39 survivors in the adrenaline group and 16 in the placebo group had severe neurological injury, by 6 months, those with severe neurological injury numbered 23 and 9, respectively. It is well established that the functional status of cardiac arrest survivors can improve over the first few months and that some with the most severe neurological injury will die. 164 Ultimately, long-term follow-up at 12 months after cardiac arrest is ideal, but is challenging because of the resources required and the increasing loss to follow-up over time, which results in attrition bias. Data on 30-day survival were available for 4012 and 3995 patients in the adrenaline and placebo groups, respectively; by 6 months, these numbers had decreased to 4006 and 3991 for the adrenaline and placebo groups, respectively, representing a loss to follow-up for survival of just six and four patients, respectively. However, neurological outcome is more difficult to collect after hospital discharge. Data on neurological outcome at discharge were available for 4007 and 3994 patients in the adrenaline and placebo groups, respectively, but, by 6 months, these numbers had decreased to 3991 and 3973, respectively, which is a loss to follow-up for neurological outcome of 16 and 21 patients, respectively. A series of sensitivity analyses were undertaken to explore the potential impact of these missing data; the results of most of these were consistent with the main results.

Patients, clinicians and researchers prioritised health-related quality of life as a core outcome for evaluation following cardiac arrest. 165 In PARAMEDIC2, health-related quality of life was impaired among survivors at 3 and 6 months, compared with the UK general population, suggesting large differences between the well-being of OHCA survivors and that of the general population. Moreover, a reduction in both mental and, to a lesser extent, physical well-being was observed at 6 months, highlighting the importance of detailed assessment over the longer term. Impairment spanned physical and mental health domains, leading to reduced health utility scores. Compared with other studies,166 the extent of functional impairment is greater, which is likely to be reflective of the PARAMEDIC2 cohort involving only patients refractory to initial attempts at resuscitation. Although there were no pronounced differences between the adrenaline and placebo groups, the overall level of impairment highlights an unmet need for this group of patients.

Meta-analyses of the PARAMEDIC2 and PACA56 trials were, as expected, consistent with adrenaline increasing survival to hospital admission (RR 2.51, 95% CI 1.67 to 3.76; two studies, 8489 participants; an increase in the rate of ROSC at hospital admission from 83 to 209 per 1000, 95% CI 139 to 313) and survival to hospital discharge (RR 1.44, 95% CI 1.11 to 1.86; two studies, 8538 participants; an increase in survival to hospital discharge from 23 to 32 per 1000, 95% CI 25 to 42). Survival rates with a favourable neurological outcome at discharge were similar (RR 1.21, 95% CI 0.9 to 1.62; two studies, 8535 participants; an increase from 19 to 22 per 1000, 95% CI 17 to 30). 55

A meta-analysis of the PARAMEDIC2 trial with the PACA56 trial according to initial cardiac arrest rhythm found very low survival-to-discharge rates with an initial non-shockable rhythm, but a significant effect for adrenaline (0.39% for placebo vs. 1.03% for adrenaline; OR 2.57, 95% CI 1.36 to 4.83). For shockable rhythms, although survival rates were higher (9.43% vs. 11.66% in placebo and adrenaline groups, respectively), the incremental effect of adrenaline was less pronounced (OR 1.26, 95% CI 0.93 to 1.71; between-group heterogeneity p = 0.05). A similar pattern was observed for survival to discharge with a favourable neurological outcome, but the CI for the OR crossed 1 for both shockable and non-shockable rhythms. 167

Two explanations for the much higher rate of ROSC and survival to hospital admission with adrenaline, and yet no significant improvement in neurological outcome, are as follows: (1) the heart is much more resilient than the brain when exposed to a period of hypoxia-ischaemia – thus, the heart can be ‘restarted’ but the brain has already been damaged irreversibly; and (2) even though adrenaline increases coronary and cerebral perfusion pressure,40 it may reduce microcirculatory flow in the brain. 29,66

Minimum clinically important difference

An international survey of key respondents from 46 countries identified that the minimal clinically important difference for survival with a favourable neurological outcome is 3% (when the baseline rate for the population is 2%). 168 Other trials have used minimal clinically important differences of 1.4%,169 2%56,170 or larger (6.3%). 171 The Universal Termination of Resuscitation Rule uses a false-positive threshold of 1%, whereas neuroprognostication algorithms172 in intensive care allow a false-positive rate for a favourable neurological outcome of up to 5%. 91,173 The 6-month difference for survival (0.8%, 95% CI 0.1% to 1.5%) and survival with a favourable neurological outcome (0.5%, 95% CI –0.1% to 1.1%) fall below the thresholds set for a minimal clinically important difference in previous studies.

Clinical effectiveness in the context of the chain of survival

The chain of survival describes the system of care required to optimise survival after OHCA. 9 It comprises four links: early access (identifying cardiac arrest early and activating the emergency services), early CPR (to maintain perfusion to the brain and vital organs), early defibrillation (to restart the heart for patients with an initially shockable rhythm) and early post-resuscitation care. The primary PARAMEDIC2 trial publication174 reported that 112 patients would need to be treated with adrenaline to prevent one death after cardiac arrest. This is substantially more than the number needed to be treated with other interventions delivered earlier in the chain of survival,175,176 for example early recognition of cardiac arrest, number needed to treat = 11;177 bystander CPR, number needed to treat = 15;178 and rapid defibrillation, number needed to treat = 5. 179

Cost-effectiveness

Economic evaluations in cardiac arrest research are relatively sparse. An economic model for public-access defibrillation reported an ICER of US$53,797 per QALY gained. 159 An economic evaluation of a mechanical chest compression device found that manual CPR dominated in health economic terms (mechanical CPR cost more and led to a reduction in QALYs, on average). 136 An extracorporeal CPR strategy in Sydney reported an ICER of €16,890 per QALY gained. A nurse-led post-cardiac arrest neurorehabilitation programme found a mean health benefit (0.04 additional QALYs) for minimal additional costs (€89), giving a 76% probability that the intervention would be cost-effective at a cost-effectiveness threshold of €80,000. 180 The NICE methods guideline132 manual notes that, in general, interventions with an ICER of < £20,000 per QALY gained are considered to be cost-effective. ICER values of > £30,000 per QALY gained require consideration of the certainty of the ICER and evidence that the assessment of the change in the health-related quality of life is inadequately captured and that the intervention adds demonstrable and distinct substantial benefits that may not have been adequately captured in the measurement of health gain.

In the present study, the ICER for the base-case analysis is 55-fold higher than the accepted cost-effectiveness threshold of £30,000. There was a low probability of cost-effectiveness (< 1%) up to a threshold of £200,000 per QALY gained. Subgroup analyses covering cause of cardiac arrest, age, sex, ambulance response time, time to drug administration, initial rhythm, witness status and bystander CPR did not identify any specific subgroups for which the ICER substantially improved. Sensitivity analyses that included societal costs, QALYs based on mRS values, a 12-month time horizon, a 12-month time horizon and societal perspective, and a 12-month time horizon and QALYs based on mRS showed that the average INMB value is always < £0.

Furthermore, our separate decision-analytic model demonstrated that the survival benefits associated with adrenaline generate additional QALY benefits, and therefore improved cost-effectiveness, over an extended time horizon. Nevertheless, even over a lifetime time horizon, the mean ICER associated with adrenaline exceeds cost-effectiveness thresholds widely accepted by decision-makers and health technology assessment agencies. Alternative extrapolations of cost-effectiveness, beyond the parameters of the PARAMEDIC2 trial, that focus solely on individuals experiencing OHCA are unlikely to alter decisions to recommend adrenaline on cost-effectiveness grounds.

It is possible that some benefits of admission to intensive care following cardiac arrest were incompletely captured through focusing on survival and health-related quality-of-life outcomes. The prevalence of post-traumatic stress among relatives of patients who die from cardiac arrest is high. 181,182 It is possible that admission to hospital allows the family time to say goodbye and to be present at the time of death. 183 Whether or not this has a beneficial effect, and any economic gains therein, remains to be determined. Approximately 10% of patients who die in ICU following OHCA become solid organ donors. 184 This may yield additional economic and health-related quality-of-life gains to the organ recipient and is worthy of further evaluation.

Ethics considerations

The design and conduct of this trial required particularly careful ethics consideration, given the life-threatening and emergency nature of OHCA. The lack of conclusive evidence of benefit, uncertainty about potential harm from adrenaline, and the presence of clinical equipoise provided the ethics justification of the need for a placebo-controlled trial. The implementation of the trial generated public debate on the ethics implications of conducting research in emergency situations without prior consent from participants or their legal representative. The public information strategy and process for enabling people to register their wish not to participate that we developed is, so far as we are aware, the first such initiative in the UK.

The implications of the trial findings for patients, clinicians, policy-makers and commissioners of health care also require careful ethics consideration. How an individual balances the chance of survival with the chance of having severe neurological impairment will be shaped by their personal values, but in the moment of a cardiac arrest, it is not possible to take into account these values when making a treatment decision. Thus, the decision about whether or not adrenaline is given will be directed by a policy or guideline applicable to all patients, informed by available evidence. A further consideration for policy-makers and commissioners of health care is the overall cost and cost-effectiveness of any treatment. The NHS is a publicly funded health service with limited financial resources and an obligation to distribute these resources fairly for everyone in response to health-care need. Our health economic analysis suggests that adrenaline treatment would not meet the current NICE criteria for cost-effectiveness. Developing a policy recommendation for the use of adrenaline for OHCA requires a complex balancing of current clinical practice norms, empirical evidence, and values. Understanding the range of population perspectives regarding this decision will be an important element of developing such a policy.

Interpretation by the International Liaison Committee on Resuscitation

The ILCOR is a collaboration of resuscitation councils from around the world that collaborate to ‘save more lives globally through resuscitation’,185 through the use of transparent evaluation of scientific data to promote, disseminate, and implement international consensus guidelines for resuscitation and first aid. The publication of the PARAMEDIC2 trial prompted the ILCOR to prioritise a review of vasopressors as treatment for cardiac arrest. 186 The ILCOR commissioned a systematic review and meta-analysis focusing on the use of standard-dose adrenaline (1 mg), compared with placebo, vasopressin, or adrenaline and vasopressin. 187 Similar to our Cochrane review,55 the review found moderate-quality evidence that adrenaline improves the rate of ROSC, survival to hospital discharge and 3-month survival among those experiencing OHCA. Subgroup analyses found that the improvement in short-term outcomes was more pronounced for non-shockable rhythms. The systematic review authors noted, in the pooled analysis, no improvement in mid-term (hospital discharge) neurological outcomes, but interpret it as showing a signal towards improved outcomes for 3-month survival, based on the findings from the PARAMEDIC2 trial [2.1% (82/3986) in the adrenaline group, compared with 1.6% (63/3979) in the placebo group; RR 1.30, 95% CI 0.94 to 1.80; absolute risk difference: 5 more per 1000 people, 95% CI 1 fewer to 13 more]. The authors acknowledge the loss to follow-up and very low event rates, leading to very low confidence in the effect estimate.

The ILCOR Advanced Life Support Task Force assessed the findings from the systematic review using the Grading of Recommendations Assessment, Development and Evaluation (GRADE) Evidence to Decision Framework. 188 The Task Force comprised 19 health-care professionals from around the world. No patient or public representatives participated in the Evidence to Decision Famework or in the development of treatment recommendations. The assessors considered the problem of OHCA as high priority. After considering the effect of adrenaline on ROSC, survival and neurological outcomes, the assessors judged the desirable effects of using adrenaline as moderate and judged the undesirable effects as small. The overall certainty of evidence was assessed to be moderate, noting that certainty varies according to outcome (high for ROSC, low for neurological outcomes). The ILCOR assessed that there was possibly important uncertainty or variability in how much people value the main outcomes, noting that the Core Outcome Set for Cardiac Arrest investigators reported that patients valued survival with favourable neurological outcome most highly. 165 The ILCOR’s overall judgement of the balance between desirable and undesirable effects probably favours using adrenaline. They reported that the intervention was probably acceptable to key stakeholders and considered it feasible to implement, noting that, although there was no research identified about patient acceptability, adrenaline use is currently the standard of care in many settings.

The writing group concluded by recommending that adrenaline should be administered as soon as possible during CPR (strong recommendation for non-shockable rhythms, weak recommendation for shockable rhythms). 186

London Ambulance Service NHS Trust

• Alexander Boda (Research Paramedic).

• Joshua Golding (Research Paramedic).

• Johanna Lazarus (Research Paramedic).

• Helen Werts (Research Paramedic).

North East Ambulance Service NHS Foundation Trust

• Emma Bell (Research and Development Assistant).

• Sonia Byers (Research and Development Manager).

• Michelle Jackson (Research Administrator).

• Matt Limmer (Research Paramedic).

• Gary Shaw (Research Paramedic).

• Craig Wynne (Research Paramedic).

South Central Ambulance Service NHS Foundation Trust

• Nikki Brock (Research Paramedic).

• Ed England (Pharmacy Advisor and Research Lead).

• Claire Godfrey (Research Paramedic).

• Claire King (Research Paramedic).

• Isabel Rodriguez-Bachiller (Research Paramedic).

• Sarah Taylor (Research Administrator).

• Michelle Thomson (Research Paramedic).

• Marie Stevens (Research Paramedic).

Welsh Ambulance Service NHS Trust

• Jennifer Bradley (Research Paramedic).

• Laura Galligan (Research Officer).

• Robert Lovett (Research Support Officer).

• Richard Whitfield (Research and Development Manager).

West Midlands Ambulance Service University NHS Foundation Trust

• Rhiannon Boldy (Clinical Audit and Research Assistant).

• Emma Harris (Clinical Audit and Research Assistant).

• Jenny Lumley Holmes (Clinical Audit Manager).

• Prudence Horwood (Research Nurse).

• Mindy Jhamat (Research Paramedic).

• Madison Larden (Research Nurse).

• Garry Parcell (Research Paramedic).

• Alice Pretty (Clinical Audit and Research Assistant).

• Gill Price (Research and Development Manager).

• Jenny Sears Brown (Research Paramedic).

Trial Steering Committee

• Robert Andrews (Member).

• Father Neil Baylis (Member).

• Jonathan Benger (Member).

• Bob Ewings (Member).

• Matthew Gane (Member).

• Stephen Jarvis (Member).

• Claire Kenna (Member).

• William Lee (Member).

• Jon Nicholl (Chairperson).

• David Pitcher (Member).

• Helen Snooks (Member).

• Matt Wise (Member).

Data Monitoring Committee

• Marion Campbell (Chairperson).

• Sue Mason (Member).

• Kathy Rowan (Member).

• Jasmeet Soar (Member).

Sponsor representative

Sponsor: Ms Jane Prewitt (Warwick Medical School, University of Warwick).

University of Warwick Clinical Trials Unit

• James Buck (Recruitment Facilitator).

• Nicola Cashin (Data Entry Clerk).

• Louise Clarkson (Clinical Trial Monitor).

• Matthew Cooke (Co-Investigator).

• Claire Daffern (Quality Assurance Manager).

• Sarah Duggan (Clinical Trials Unit Manager).

• Hayley Johnson (Trial Administrator).

• Programming team.

• Malvenia Richmond (Data Entry Clerk).

• Sarah Rumble (Clinical Trials Co-ordinator).

• Natalie Strickland (Clinical Trials Unit Manager).

• Martin Underwood (Clinical Trials Unit Director).

• Eva Vernon (Trial Co-ordinator).

• Jill Wood (Quality Assurance Manager).

MODEPHARMA Ltd (Beckenham, UK)

• Oliver Gupta (Project Manager – IMP supplies).

• Rima Gupta (Project Manager – IMP supplies).

We would like to thank the patients and legal representatives.