Antimicrobial-impregnated central venous catheters for preventing neonatal bloodstream infection: the PREVAIL RCT

Aims

The overall aim of the study was to determine whether or not antimicrobial-impregnated PICCs (AM-PICCs) should be adopted across the NHS for babies receiving neonatal care. We undertook three inter-related analyses to address this aim (see Figure 1):

1. a clinical effectiveness RCT – to determine the clinical effectiveness of AM-PICCs, compared with standard PICCs (S-PICCs), for babies receiving neonatal care

2. an economic analysis – to determine the cost-effectiveness of AM-PICCs, compared with S-PICCs, from an NHS perspective

3. a generalisability analysis – to generalise the trial results to neonatal care in the NHS in England.

Objectives

Generalisability analysis

The objectives of the generalisability analysis were as follows:

• to determine generalisability and applicability by comparing BSI risk factors, causative organisms and rates of BSI among babies in the PREVAIL trial with other babies receiving PICCs

• to determine the applicability of BSI rates in the PREVAIL trial to rates of BSI in the NHS in England by comparing trends in BSI in babies receiving PICCs in the PREVAIL trial neonatal intensive care units (NICUs), non-PREVAIL trial NICUs and local neonatal units (LNUs)

• to provide context through understanding of changes in BSI over time by evaluating trends in rates of late-onset BSI per 1000 days of intensive or high-dependency care and per 100 admissions for all babies receiving intensive or high-dependency care in NICUs and LNUs

• to determine the contribution of PICCs to the overall rate of BSI per admission.

The data source was the NNRD linked to national laboratory infection surveillance data for England.

The three components of the study are illustrated in Figure 1. We also considered further uses of these linked data. First, for ongoing monitoring of BSI rates following implementation of an effective intervention. Second, to link trial and linked administrative health data to school achievement data to assess long-term effects of PICC impregnation on cognitive ability measured in school achievement assessments. These uses have not been pursued, because the infection outcome in the randomised groups did not differ.

FIGURE 1.

Flow diagram to show inter-relationship between the three components of the PREVAIL study.

Ethics approval and research governance

The protocol was approved by the Yorkshire and the Humber Health Research Authority (reference number 14-YH-1202). The trial was funded by the National Institute for Health Research (NIHR) Health Technology Assessment programme and included in the International Standard Randomised Controlled Trial Number registry [https://doi.org/10.1186/ISRCTN81931394 (accessed 22 July 2020)]. Centre-specific approval was obtained at all recruiting centres.

Full details of the amended trial protocol (version 5.0, 26 April 2017), the research ethics approval and the statistical analysis plan are available online [http://prevailtrial.org.uk/ (accessed 22 July 2020)].

A summary of substantial protocol amendments is provided in Appendix 1, Table 26.

Selection of trial sites

Recruitment took place in 18 out of 43 NICUs in England. Overall, there are 154 NNUs in England (Table 2), of which 43 are NICUs that provide intensive care for babies, such as invasive ventilation and organ system support (Table 3). Days of intensive care are supported by nurse staffing ratios of one nurse to one baby, with step-down care for high-dependency (one nurse to two babies) and special care (one nurse to four babies). 51 Of the 154 NNUs, 76 LNUs provide short-term intensive care and high-dependency and special care, and 35 NNUs provide special care only [i.e. special care baby units (SCBUs)]. One in 10 babies admitted to a NNU is transferred to another unit for higher or lower levels of care. Step-up transfers between NNUs within neonatal networks are used to provide centralised intensive care when needed, including neonatal surgery for a small proportion of babies. Step-down transfers are frequently used to allow babies to be cared for near to parents and to reduce pressure for beds in NICUs. Low-intensity neonatal care is also provided in transitional care wards, which are not considered here.

We invited expressions of interest from NNUs in 2015. We prioritised NICUs with the largest number of babies born before 32 weeks of gestation, using NNRD data, and those sites invited to participate through the Children’s Clinical Research Network.

Participants

Eligible participants were all babies who required the narrowest (1 French gauge) PICC. Only babies who had previously participated in the trial or who were known to have an allergy or hypersensitivity to rifampicin or miconazole were excluded.

The reason for insertion was not requested, but PICCs are primarily used for parenteral nutrition, particularly in preterm babies. As this was a pragmatic trial, designed to reflect routine practice, we did not restrict eligible participants to preterm babies. However, in practice, the 1-French gauge PICC is predominantly used in preterm babies born before 32 weeks of gestation, as more mature and larger babies normally require a wider-gauge PICC to infuse sufficient volumes of fluid. Preliminary, unpublished analyses using the NNRD revealed that 70% of babies in neonatal units born before 32 weeks of gestation had a PICC inserted (unpublished data, NNRD, England).

Screening

The principal investigator (PI) or research nurse (RN) maintained a screening log of babies whose parents were approached about the trial, detailing reasons for declining consent or reasons for no randomisation occurring for those who did consent. They also kept a log of all babies who received a PICC [a 1-French Premicath^®; Vygon (UK) Ltd], but whose parents were not approached for the trial, and why they were not approached.

Enrolment

When a baby was likely to require a PICC (Premicath, 1 French), the clinician or RN provided written information and met with the parents to discuss participation in the trial. 52 Written consent was required, along with confirmation of eligibility from the PI or designated other before randomisation could occur. Twins were treated as separate individuals for consent and randomisation, if both babies required a PICC. Babies could be simultaneously enrolled in multiple studies, as agreed between chief investigators.

Randomisation, concealment and blinding

Participants were randomised to either an AM-PICC or a S-PICC using a secure web-based randomisation programme by the PI or delegated other at each of the 18 recruitment sites. PICC insertion was scheduled to occur within 48 hours of randomisation by a designated staff member. Randomisation sequences were computer-generated by an independent statistician in random, variable blocks of two and four, stratified by site. Randomisation was controlled centrally by the Liverpool Clinical Trials Centre (LCTC), at the University of Liverpool (UoL), to ensure allocation concealment. It was impractical to mask clinicians to PICC allocation because rifampicin caused brown staining of the AM-PICC. Participant inclusion in analyses and occurrence of outcome events were determined by following an analysis plan that was specified before individuals saw unblinded data.

Baseline characteristics

We recorded the following demographic and relevant clinical characteristics at randomisation.

• demographics – sex, birthweight, gestational age at birth and age at randomisation

• delivery characteristics – born in the trial hospital or transferred to the trial hospital after birth, vaginal or caesarean delivery, ruptured membranes > 24 hours before birth, maternal antenatal steroids received or not, and maternal antibiotics received within 12 hours pre delivery

• characteristics of neonatal care before randomisation – surgery in the previous 14 days, samples taken, antimicrobial medication received and the highest level of respiratory support required, all within the previous 72 hours

• other clinical characteristics – major congenital anomaly; appearance, pulse, grimace, activity, respiration (Apgar) score at 5 minutes of age; number of invasive devices in situ; and the site where the randomised PICC was successfully inserted.

Adherence to treatment and the protocol

To measure adherence to the intervention, we recorded whether or not a PICC was inserted, and, if so, whether or not it was the allocated PICC, the reasons for removal, the length of time that the PICC was in situ, and whether or not positive samples were tested for resistance.

Protocol deviations were monitored centrally via evaluation of inclusion/exclusion criteria at trial entry and throughout the course of the trial. Some of the secondary outcomes (see the following sections) were also designed to detect potential biases in adherence to the trial protocol that might be influenced by knowledge of the type of PICC.

Primary outcome

The primary outcome was time from randomisation to first bloodstream or CSF infection, defined as a microbiological culture of a bacteria or fungus from blood or CSF sampled for clinical reasons. We use the term BSI to refer to a positive culture from blood or CSF. We defined the primary outcome time window as the period when any positive blood or CSF cultures could be counted in the primary outcome. The time window was from 24 hours post randomisation until 48 hours after PICC removal or death (or 48 hours after randomisation if the PICC was not inserted; see Figure 2). We imposed a priori decision rules to avoid counting pre-existing BSI. We excluded microbial cultures that were within the time window if the same organism was isolated from blood or CSF and samples were taken < 14 days apart, or if a different organism was isolated and samples were < 24 hours apart. When there were multiple positive cultures within the primary outcome time window, each positive culture was assessed and the first one that met the definition was counted.

Secondary outcomes

Safety outcomes

All AEs (expected and unexpected) considered to be related to the PICC were reported until 48 hours after PICC removal.

General statistical considerations

The analysis and reporting of the trial were undertaken in accordance with the Consolidated Standards of Reporting Trials (CONSORT)55,56 and the International Conference on Harmonisation E9 Guidelines. 57 The main features of the statistical analysis plan are included in this section, with a full and detailed statistical analysis plan provided as a supplementary file58 on the PREVAIL trial website.

Outcome data were analysed according to the intention-to-treat principle, which is including all randomised participants in the group to which they were allocated (regardless of whether or not the allocated PICC was inserted) and for whom the outcome was measured/observed. All statistical tests were two-sided and performed using a 5% significance level. We used 95% CIs throughout. There were no adjustments for multiple testing; rather, all secondary analyses were treated as hypothesis-generating.

All analyses were conducted with SAS^® version 9.4 (SAS Institute Inc., Cary, NC, USA). Results from the primary outcome and safety analyses were validated by independent programming by another statistician from the point of raw data.

Baseline characteristics

Demographics and other clinical baseline characteristics were summarised for each treatment group and overall, using descriptive statistics. No formal statistical testing was performed on these data. Descriptive statistics, including the number of observations, mean and standard deviation (SD) for continuous variables, and counts and percentages for discrete variables, were presented as appropriate.

Adherence to treatment and the protocol

All protocol deviations were agreed with the co-chief investigators prior to them seeing any unblinded results. These data were summarised for each treatment group and overall, using descriptive statistics, as for the baseline data. No formal statistical testing was performed on these data.

Primary outcome

The primary outcome, time to first BSI, was measured from randomisation to the first sample that met the definition of an independent episode of BSI. Participants not experiencing the primary outcome were censored at death, 48 hours after PICC removal or 48 hours after randomisation (for those with no PICC inserted). The difference between the groups was tested using the log-rank test, and the hazard ratios (HR) and associated 95% CIs obtained from the Cox proportional hazards model were presented. Kaplan–Meier curves were used to present the number of babies at risk. The number of samples taken, the number of babies with samples taken and the number of babies with a BSI within the primary outcome time window were also presented for each treatment group, overall and split by sample type.

Four sensitivity analyses of the primary outcome were prespecified to determine the robustness of the results of the primary analysis:

1. time from randomisation to first clinically serious BSI, defined as treatment with antimicrobials for ≥ 72 hours or death during treatment

2. time from PICC insertion to first BSI

3. time from randomisation to first BSI excluding samples obtained via arterial cannulas or CVCs

4. time from randomisation to first BSI including only clearly pathogenic organisms, as defined in Appendix 1, Table 27.

After seeing the results, we specified an additional analysis of the primary outcome to investigate whether or not the treatment effect varied by gestational age at birth (< 28 weeks or ≥ 28 weeks of gestation at birth) using a Cox proportional hazards model, including an interaction between treatment and gestational age.

Secondary outcomes

Safety analyses

The statistical analysis plan specified that all babies who had a PICC inserted or who had an attempted insertion would be included in the safety analysis population. The plan specified that babies who had a PICC inserted would be analysed according to the treatment they received, and that babies for whom PICC insertion was attempted but unsuccessful would be analysed according to the allocated treatment group, as information was not recorded on the type of PICC that was used for attempted insertion. However, after seeing the trial results, it was deemed more appropriate to exclude babies in whom insertion was unsuccessful from the safety analysis population.

All AEs and serious adverse events (SAEs) reported by the clinical investigator and classified as ‘possibly’, ‘probably’ or ‘almost certainly’ related to the trial treatment were presented. The number (and percentage) of occurrences of each AE/SAE and of babies experiencing each AE/SAE were presented for each treatment arm. The same information was also presented split by severity. For each baby, only the maximum severity that they experienced for each type of AE was displayed. No formal statistical testing was undertaken.

Trial Management Group

The TMG comprised the co-chief investigators, specific co-investigators (clinical and non-clinical), members of the LCTC and members of the chief investigator’s team at University College London (UCL). The TMG was responsible for the month-to-month management of the trial. The TMG proposed the membership of the oversight committees [the TSC and the Independent Data and Safety Monitoring Committee (IDSMC)] to the trial funders, who then made appointments according to their constitutional requirements. Members are listed in the Acknowledgements.

Trial Steering Committee

The TSC consisted of an independent chairperson, an independent expert in the field of neonatology, an independent statistician and a parent representative. One of the co-chief investigators was a non-independent member of the TSC. The TSC was the executive decision-making committee considering the recommendations of the IDSMC. Monitoring reports viewed by the TSC did not present data split by treatment group. Members are listed in the Acknowledgements.

Independent Data and Safety Monitoring Committee

The IDSMC included an independent chairperson, an expert in the field of microbiology and an independent statistician. The IDSMC was responsible for reviewing and assessing recruitment and for interim monitoring of safety and effectiveness, trial conduct and external data. The IDSMC provided recommendations to the TSC concerning the continuation of the trial. Members are listed in the Acknowledgements.

Role of the funding source

The funder appointed independent members to the TSC and the IDSMC, approved all protocol amendments and monitored study progress against agreed milestones. The funder had no involvement in data interpretation or writing of the report. The corresponding author had full access to all outputs from the data in the study.

Dual publication

Chapters 1 and 2 contain information published in the 2019 report of the PREVAIL trial findings, with further details and results. 1 Chapter 2 includes details reported in the PREVAIL trial protocol and statistical analysis plan, which have already been published on the PREVAIL website. 58,59

Baseline characteristics

The two treatment groups were comparable in terms of baseline characteristics (Tables 4–7). Of the 861 babies who were randomised, 715 (83%) were randomised before 7 days of age and 754 (88%) were born before 32 weeks of gestation.

Adherence to treatment and the protocol

Fewer babies randomised to the AM-PICC had the randomly allocated PICC inserted [373 participants (86.7%)] than those randomised to the S-PICC group [407 participants (94.4%)] (Table 8). Approximately half of the babies who did not receive the allocated AM-PICC had no PICC inserted, and half received a different PICC.

The intention-to-treat analysis population included all 861 participants (100%) who were randomised, regardless of whether or not they received the allocated PICC. The safety population as defined in the statistical analysis plan (all participants in whom insertion was successful or attempted) included 842 of the 861 randomised participants (97.8%). The modified safety analysis (all participants in whom insertion was successful) included 816 of the 861 randomised participants (94.8%) (see Table 8 for further details on which participants were included in the safety analysis populations).

The time points for end of follow-up were similar in both groups (see Table 8). The majority of participants completed follow-up for infection outcomes (outcomes for which samples were required to be taken) 48 hours after removal of the PICC [785/861 (91.2%)] and follow-up for other outcomes at discharge home from neonatal care [768/861 (89.2%)].

The type and frequency of sampling for microbiological cultures were similar in both groups (see Appendix 2, Table 35); blood/CSF samples were taken from 198 babies in the AM-PICC group (46.0%) and from 190 babies in the S-PICC group (44.1%). The frequency of testing for rifampicin resistance in blood or CSF positive cultures was slightly lower in the AM-PICC group than in the S-PICC group, but similar for PICC tips, although there were half as many positive cultures from PICC tips in the AM-PICC group [47 participants (10.9%)] as in the S-PICC group [90 participants (20.9%)].

Protocol deviations were generally similar across the two treatment groups (see Appendix 2, Table 36). A total of 86 participants (10.0%) had at least one major protocol deviation. The most common major deviation was not receiving the allocated PICC [81 participants (9.4%)], and the most common minor deviations were the PICC tip culture not being taken at removal [167 participants (19.4%)] and resistance testing not being done on positive cultures [135 participants (15.7%)].

Primary outcome

A total of 46 participants in the AM-PICC group (10.7%) and 44 participants in the S-PICC group (10.2%) experienced a BSI in the primary outcome time window. The median time to BSI could not be calculated as not enough participants experienced an event. The time from randomisation until first BSI did not differ between the groups (HR 1.11, 95% CI 0.73 to 1.67) (Table 9 and Figure 4). The Kaplan–Meier curves crossed when the numbers at risk were low. A time-varying coefficient was added to the model to check the assumption of proportional hazards; this was not significant (p = 0.62).

FIGURE 4.

Kaplan–Meier plot: time to first BSI (primary outcome). The table under the graph presents the numbers of study participants at risk (i.e. not censored) at each time point.

The results from all four sensitivity analyses are consistent with the results from the primary analysis, indicating that the original results are robust regarding the assumptions that were made (see Table 9). The post hoc analysis that was performed to determine if there was evidence of a difference in treatment effect for babies with a gestational age of < 28 weeks compared with babies with a gestational age of ≥ 28 weeks found that this was not the case (p = 0.28). Appendix 2, Figures 16 and 17 show further results from the post hoc analysis.

Secondary outcomes

Safety analysis

All related AEs in participants who had a 1 French PICC successfully inserted are listed in Table 14. A total of 60 events were reported from 49 participants in the AM-PICC group (13.1%), and 50 events were reported from 45 participants in the S-PICC group (10.5%).

One SAE involving supraventricular tachycardia following PICC placement was reported in the AM-PICC arm. This event met the seriousness criterion of ‘medically significant’, and the local investigator felt that it was ‘possibly’ related to the recent insertion of the PICC. The event resolved and the PICC was not removed. This event was assessed as ‘unlikely’ to be related to the trial intervention by the chief investigator, but was reported to the Medicines and Healthcare products Regulatory Agency Adverse Incident Centre in line with the local investigator’s assessment.

Background

This section estimates the cost of hospital care for babies taking part in the PREVAIL trial (hereafter termed ‘PREVAIL babies’) for whom routine health-care data were available and whose parents had consented for their data to be shared with the research team.

Methods

Overview

Figure 5 summarises the methods. The PREVAIL babies may have received a variety of hospital care during the 6-month follow-up period. We sought data on hospitalisations from different data sources, which included stay in the NNU, admission to a PICU, admissions to paediatric hospital care, procedures such as surgery and diagnostic tests, outpatient appointments, and visits to the A&E department. We obtained data on the nature and intensity of hospital care in these different settings and used it to generate standardised units of cost called Healthcare Resource Groups (HRGs). We obtained the unit costs of the HRGs from NHS reference costs 2015–16,62 which represent their average cost to the NHS. The cost of hospital care for each baby is the sum of the costs of the HRGs.

FIGURE 5.

Overview of the methods used to estimate the cost of hospitalisations.

Results

Background

The primary objective of the cost-effectiveness analysis was to estimate the long-term costs and health benefits of using AM-PICCs, compared with using S-PICCs, in babies in the NICU. The PREVAIL trial provided data on the risk of BSI, the AM-PICC effectiveness and the hospital costs over 6 months of babies who received AM-PICCs, compared with babies who received S-PICCs. To estimate the costs and health benefits of using an AM-PICC or a S-PICC over a baby’s lifetime, information was needed on the long-term consequences of using each PICC. This information was obtained from the published literature and synthesised in a de novo cost-effectiveness model. This section reports the methods used to develop the cost-effectiveness model and the results of the cost-effectiveness analysis.

The model was developed to evaluate the cost-effectiveness of any intervention for the prevention of infection in neonates in the NNU. For the purposes of the cost-effectiveness model, infection is an umbrella term that includes, not only BSI and clinically serious BSI, as defined in the PREVAIL trial, but also sepsis (indicating BSI with clinical signs of tissue damage). The key assumption of the model was that infection increases the risk of death and of developing neurodevelopmental impairment (NDI) in early childhood. NDI is associated with lower life expectancy, worse health-related quality of life (HRQoL) and higher costs to the NHS. 71 Consequently, babies who had a BSI during their stay in the NNU are expected to experience worse health outcomes and higher costs because of the long-term consequences of infection. Therefore, interventions reducing the risk of infection may be cost-effective, depending on the magnitude of risk reduction and costs.

Methods

Model structure

Predicting outcomes in early childhood

The model included a short- and a long-term component. The short-term component was a decision tree. Babies enter the model at the time of PICC insertion. The model estimated the proportion of children alive at 2 years of age, and their distribution by level of NDI (none, mild, moderate or severe) (Figure 6). PICC type (AM-PICC or S-PICC) determines the probability of BSI and costs, as observed in the PREVAIL trial. BSI is assumed to increase the probabilities of death and of experiencing NDI.

FIGURE 6.

Model structure for predicting outcomes in early childhood. The square denotes the decision: use either an AM-PICC or a S-PICC. The circle denotes a probability (or chance) node. The triangle denotes when the structure is the same in both arms. The diagram details the parameter inputs; their numbers correspond to the numbers in Table 17.

Predicting lifetime costs and health outcomes beyond 2 years of age

The long-term component of the model simulated the lifetime health outcomes and costs given the children’s NDI levels. It assumed that previous BSI does not influence longer-term lifetime costs and health outcomes. The model was a Markov model,86 based on the model depicting the costs of prematurity by Mangham et al. 71 Children enter the model at 2 years of age in one of the NDI states, according to the proportion of babies computed by the decision tree (Figure 7). At each cycle, children can transition between NDI states or die. The transitions represent the improvement or deterioration in the neurodevelopmental state of the child, as well as inaccuracies in the assessment, which might become apparent over time. After reaching 8 years of age, children were assumed to no longer transition between NDI states; therefore, the only transition after age 8 years is to the absorbing death state. The risk of death depends on both age and NDI state.

FIGURE 7.

Model structure for predicting lifetime costs and health outcomes. The arrows depict the possible transitions between model states in each cycle.

Results

Predicting lifetime costs and health outcomes

Figure 8 shows the outcomes by NDI level over the children’s expected lifetime. The model predicts that children who are assessed as having no NDI at 2 years of age live to 76 years, on average (95% CI 73 to 78 years). As the NDI level increases, life expectancy reduces. Children who are assessed as having a severe NDI at 2 years of age are predicted to live to 61 years (95% CI 47 to 74 years).

FIGURE 8.

Costs and health outcomes by NDI level over expected lifetime. The NHS costs and the lifetime QALYs accrued in the future are discounted at 3.5% in line with current guidelines. The life expectancy from PICC insertion is not discounted. The vertical lines indicate the 95% CIs. Adapted from Grosso et al. 106 © Author(s) (or their employer(s)) 2020. Re-use permitted under CC BY. Published by BMJ. This is an open access article distributed in accordance with the Creative Commons Attribution 4.0 Unported (CC BY 4.0) license, which permits others to copy, redistribute, remix, transform and build upon this work for any purpose, provided the original work is properly cited, a link to the licence is given, and indication of whether changes were made. See: https://creativecommons.org/licenses/by/4.0/. Minor formatting changes have been made.

Adapted from Grosso et al. 106 © Author(s) (or their employer(s)) 2020. Re-use permitted under CC BY. Published by BMJ. This is an open access article distributed in accordance with the Creative Commons Attribution 4.0 Unported (CC BY 4.0) license, which permits others to copy, redistribute, remix, transform and build upon this work for any purpose, provided the original work is properly cited, a link to the licence is given, and indication of whether changes were made. See: https://creativecommons.org/licenses/by/4.0/. Minor formatting changes have been made.

The differences in costs and health outcomes between mild NDI and no impairment are £3690 lower costs and 2.16 additional QALYs. This means that if one child has mild NDI, then, on average, and compared with having no NDI, the child loses 2.16 QALYs over their lifetime and costs an additional £3690 to the NHS. If a QALY is valued at £20,000 by the NHS, avoiding mild NDI in one child warrants £46,890 (2.16 QALYs × £20,000 + £3690) in investment by the NHS.

Sensitivity analysis

The sensitivity analysis results are presented in detail in Appendix 11. The key results are discussed in this section.

Bivariate sensitivity analysis: effectiveness and price

At the current price, the minimum level of effectiveness at which the AM-PICC is cost-effective, at a cost-effectiveness threshold of £20,000 per QALY, is a relative reduction of 3% in the risk of BSI for babies with gestational age at birth of 23–27 weeks, that is a maximum RR of 0.97. For babies with gestational age at birth of 28–32 weeks, the minimum reduction is of 15%, that is a maximum RR of 0.85. At the cost-effectiveness threshold of £13,000 per QALY, the minimum relative reduction is 4% and 20% for babies with gestational age at birth of 23–27 and 28–32 weeks, respectively (Figure 9).

FIGURE 9.

Maximum acquisition price per AM-PICC effectiveness (gestational age at birth of 23–27 weeks). Reproduced from Grosso et al. 106 © Author(s) (or their employer(s)) 2020. Re-use permitted under CC BY. Published by BMJ. This is an open access article distributed in accordance with the Creative Commons Attribution 4.0 Unported (CC BY 4.0) license, which permits others to copy, redistribute, remix, transform and build upon this work for any purpose, provided the original work is properly cited, a link to the licence is given, and indication of whether changes were made. See: https://creativecommons.org/licenses/by/4.0/. Minor formatting changes have been made.

Reproduced from Grosso et al. 106 © Author(s) (or their employer(s)) 2020. Re-use permitted under CC BY. Published by BMJ. This is an open access article distributed in accordance with the Creative Commons Attribution 4.0 Unported (CC BY 4.0) license, which permits others to copy, redistribute, remix, transform and build upon this work for any purpose, provided the original work is properly cited, a link to the licence is given, and indication of whether changes were made. See: https://creativecommons.org/licenses/by/4.0/. Minor formatting changes have been made.

The maximum acquisition price would increase if the effectiveness increased. For example, if the AM-PICC reduced 5% of BSI cases (RR 0.95), the maximum acquisition price at a cost-effectiveness threshold of £20,000 per QALY would be £165, if used solely in babies born at 23–27 weeks’ gestation, or £65 in babies born at 28–32 weeks’ gestation. At a cost-effectiveness threshold of £13,000 per QALY, and for the same effectiveness, the maximum price would be £120 and £55 if used solely in the gestational age groups 23–27 and 28–32 weeks, respectively. At the prices currently charged for the AM-PICC, and at a cost-effectiveness threshold of £20,000 per QALY, the AM-PICC would have to reduce 2% and 15% of cases to be cost-effective for babies born at 23–27 and 28–32 weeks’ gestation, respectively. At a cost-effectiveness threshold of £13,000 per QALY, the AM-PICC would have to reduce at least 3% and 20% of cases to be cost-effective for babies born at 23–27 and 28–32 weeks’ gestation, respectively.

Complete results of this sensitivity analysis are presented in Appendix 11, Tables 71 and 72.

Univariate sensitivity analysis

For both gestational age groups considered, the key cost-effectiveness driver was the RR of the AM-PICC in preventing BSI (see Appendix 11, Figures 23 and 24).

Scenario analysis

The AM-PICC was found to be not cost-effective (i.e. negative incremental net benefit), irrespective of the scenario implemented (see Appendix 11, Table 73). In most scenarios, the incremental net benefit was similar to the base case. Large decreases in incremental net benefit were observed in the scenarios assuming that BSI increased the risk of death, and, to a smaller extent, in the scenarios assuming different hospital costs depending on whether or not death and BSI had occurred. This happens because the PREVAIL trial indicates that the AM-PICC results in a slightly higher number of BSIs (as per Table 17). In scenarios in which BSI increases the risk of death, the costs are lower because children who die do not incur subsequent hospital costs. However, there is a large loss of QALYs, owing to the increased proportion of babies who die in infancy. In these scenarios, the AM-PICC appears to be more detrimental to babies than in the base-case assumption of no direct effect of BSI on death at 6 months.

Methods

Results

Objectives

• To determine the generalisability and applicability of the trial results by comparing BSI risk factors, causative organisms and BSI rates among babies in the PREVAIL trial with those of other babies receiving PICCs.

• To determine the applicability of BSI rates in the PREVAIL trial to rates of BSI in the NHS in England by comparing trends in the rates of BSI in babies receiving PICCs in PREVAIL trial NICUs, non-PREVAIL trial NICUs and LNUs.

• To provide context through understanding of changes in BSI over time by evaluating trends in rates of BSI per 1000 days of intensive or high-dependency care and per 100 admissions for all babies receiving intensive or high-dependency care in NICUs and LNUs.

• To determine the contribution of PICCs to the overall rate of BSI per admission during intensive and high-dependency care.

The generalisability study originally aimed to predict the number of BSIs prevented and the reduction in cost to the NHS if AM-PICCs were adopted and used in place of S-PICCs. This was not feasible, because the PREVAIL trial detected no difference in the risk of BSI between AM-PICCs and S-PICCs, and, based on these results, AM-PICCs are unlikely to be adopted. A further reason is that the cost of BSI could not be calculated in the health economics study (see Chapter 4).

Data sources

There is no single data source to study risk-adjusted rates of BSI in NNUs in England. The NNRD provides clinical data on babies in NICUs. Historically, data on BSI in the NNRD was poorly completed, but entry of data on BSI is improving: 74 NNUs reported entering data on all positive cultures in 2017, compared with 25 in 2016. 16,109,110 PHE operate a national infection surveillance system, known as the Second Generation Surveillance System. We linked these two data sources to create a linked data set of babies in all available NICUs and LNUs (112/124) in England. A combination of deterministic and probabilistic linkage methods were used to link babies recorded in the NNRD to records of BSI reported to the national infection surveillance system during their NNU admission. 111 The linkage process is described in Appendix 12. In brief, deterministic links, based on an exact match on NHS number, were used as reference standards to calculate match weights in probabilistic linkage, based on agreement on postcode prefix, postcode suffix, date of birth, laboratory/hospital and sex. 112 Match weights were summed across each comparison pair and the frequency of the summed weights were examined to determine an upper and lower threshold. Pairs with weights above the upper threshold were classified as links, pairs with weights below the threshold were classified as non-links and pairs between the two thresholds were manually reviewed (using rules presented in Appendix 12, Table 74). Links identified in deterministic and probabilistic linkage were combined to produce a NNRD data set enhanced with BSI from the national infection surveillance.

Three NICUs [3/49 (6%)] and nine LNUs [9/78 (12%)] were excluded from our NNRD data. The number of NNUs changed over time: there were 49 NICUs during the generalisability study period (2010–17), but only 43 during the PREVAIL trial. Two NICUs and eight LNUs were excluded because we did not receive responses to our requests for consent to linkage of their data. One NICU and one LNU were excluded because of poor reporting of BSI in the surveillance data. A further three NICUs and six LNUs had reporting gaps in the BSI surveillance data; we excluded months when reporting was poor, but included periods with good reporting. We did not include any SCBUs and we restricted our analyses of the linked data to babies receiving intensive or high-dependency care, as PICCs are not routinely used in special care. Three LNUs became SCBUs during the trial period; they were removed when they became SCBUs. We obtained data from the NNRD in two extractions, (1) March 2010 to December 2015 and (2) January 2016 to June 2017, which resulted in missing data for babies admitted in the first extract but discharged in the second extract. More than 5% of baby days between September 2015 and December 2015 were missing a discharge date, probably due to missing records in 2016. We therefore excluded admissions during the 6 months between September 2015 and February 2016. We excluded all babies who were missing a discharge date as we were unable to correctly calculate time at risk.

Case definition

We defined BSI as a link to a record of positive blood or CSF culture reported to the national infection surveillance system. Multiple cultures of the same organism from the same baby within 14 days were classified as one episode. We use five terms to describe BSI depending on time at risk (Figure 10; see also Appendix 20, Table 81):

1. BSI during PICC days at risk, which included BSI cultured in samples taken between 1 day after PICC insertion and 2 days after PICC removal.

2. Early-onset BSI (no PICC), defined as BSI in babies aged < 2 days. If a baby had a PICC inserted on the day of birth and a BSI on the following day, the BSI would be classified as during PICC days at risk, not as early onset.

3. Late-onset BSI describes BSI from samples taken between 2 days of age and 2 days after discharge from the NICU or LNU, given that the BSI is not during PICC days at risk.

4. Total late-onset BSI included BSIs that were either during PICC days at risk or late onset.

5. Total BSI included all BSI occurring between birth and 2 days after discharge from the NICU or LNU.

FIGURE 10.

Time at risk for PICC days at risk, early-onset BSI (no PICC) and late-onset BSI (no PICC).

Our definition of PICC days at risk (see Figure 10 and Appendix 20, Table 81) differed slightly from the definition used in the trial (see Figure 2), as we used linked infection surveillance data (not BSI recorded on CRFs in the trial) to ensure comparability between PREVAIL babies and other groups. Surveillance data do not record the exact time of blood or CSF culture sampling, and the NNRD records whether or not a PICC was present each day, but not the time of insertion. Therefore, we used 1 or 2 days, rather than 24 or 48 hours, to define the interval for samples related to the PICC: 1 day after PICC insertion to 2 days after PICC removal (as recorded in the NNRD).

We categorised all organisms recorded in the surveillance data as ‘clearly pathogenic’ or ‘other’ with the guidance of a microbiologist (JG). We used the term ‘clearly pathogenic organisms’ to indicate that a BSI would be diagnosed without the requirement of repeat samples or clinical signs. A full list of clearly pathogenic and other organisms is given in Appendix 13, Boxes 2 and 3. We restricted trend analyses to clearly pathogenic organisms because of a change in the surveillance system in 2014 that resulted in a sharp increase in the reporting of organisms with uncertain clinical significance (e.g. skin commensals) (see Appendix 14, Table 75 and Figure 25).

Identifying babies in the PREVAIL trial

We linked babies who were randomised to receive S-PICCs in the PREVAIL trial to the NNRD. We used deterministic linkage on NHS number or postcode, sex and date of birth. We excluded babies randomised to receive AM-PICCs in the PREVAIL trial and any babies who had no daily records of intensive or high-dependency care, were present only in months excluded because of missing NNRD days between 2015 and 2016, were present only in months excluded because of poor BSI reporting, had missing discharge dates, or had no record of receiving a PICC. We compared the distribution of baseline baby characteristics [gestation, admission to surgical NICU, sex and small for gestational age (birthweight in the < 10th centile for gestation)] using the chi-squared test to determine whether or not there was a significant difference (p < 0.05) between included and excluded PREVAIL babies.

Generalisability and applicability

To determine the generalisability of results of the PREVAIL trial to other babies in NICUs, we compared babies admitted to NICUs who were randomised to receive S-PICCs in the PREVAIL trial with babies who received S-PICCs in the PREVAIL trial NICUs who were not enrolled in the trial, and those in non-PREVAIL trial NICUs, during the recruitment period. Approximately 10% of babies were admitted to more than one NICU or LNU. We evaluated admissions to NNUs, rather than evaluating babies, to ensure that BSI, PICC days and other clinical factors were attributed to the correct NICU or LNU. To determine applicability, we extended the comparison of PREVAIL babies to babies receiving S-PICCs in LNUs during the recruitment period. We compared the prevalence of baby and clinical characteristics, causative organisms and the rate of BSI per 1000 PICC days during the PREVAIL trial recruitment period (August 2015 to January 2017). We used the start and end date specific to each participating NICU, as these dates varied between units. For non-PREVAIL trial NICUs and LNUs, we included the total recruitment period. We also compared trends in rates of BSI per 1000 PICC days from March 2010 to June 2017.

Trends in rates of bloodstream infection in all babies admitted to neonatal intensive care units and local neonatal units

To contextualise the trial, we extended the analyses to include all babies who received intensive and high-dependency care in NICUs and LNUs, regardless of whether they received a PICC. First, we examined how BSI risk factors had changed from 2010 to 2017 for all babies who received high-dependency or intensive care in LNUs and NICUs. Second, we evaluated trends in total late-onset BSI per 1000 days of intensive and high-dependency care days and per 100 admissions.

The contribution of peripherally inserted central venous catheters to total bloodstream infection

We calculated the proportion of total BSI that was early onset (no PICC), during PICC days at risk or late onset (no PICC). We included BSI caused by all organisms for the period of August 2015 to June 2017. We excluded the period before the start of the PREVAIL trial to give an up-to-date snapshot of recent BSI and to ensure that results were not affected by the change in surveillance methodology in 2014. To determine the contribution of PICCs to the overall rate of BSI per admission, we first calculated the BSI rate per admission for early-onset BSI (no PICC), BSI during PICC days at risk and late-onset BSI (no PICC), for all babies admitted to NICU or LNUs and stratified by gestation at birth (< 32 or ≥ 32 weeks).

Identifying babies in the PREVAIL trial

We identified 423 babies in the NNRD out of the 431 babies recorded as randomised to receive the S-PICC in the PREVAIL trial CRFs. All babies randomised to receive the AM-PICC in the PREVAIL trial were excluded from the generalisability analyses using linked data from the NNRD. We included 269 out of 423 (64%) babies randomised to S-PICCs (see Appendix 21, Figure 26). The reasons for excluding 154 babies were as follows: present only in months excluded because of missing days between 2015 and 2016 (n = 97), present only in months excluded because of poor BSI reporting (n = 24), missing discharge dates (n = 2) and no recording of PICCs (n = 31). Only 16 babies randomised to S-PICCs were recorded as not receiving a PICC in the PREVAIL trial CRFs. Therefore, 15 of the 31 babies with no PICC recorded in the NNRD (4% of the total of 423 babies) had a PICC recorded in the trial CRFs but not in the NNRD. There were no significant differences in the distributions of gestation, small for gestational age or sex between the 269 babies with S-PICCs included in our analysis and the 154 excluded PREVAIL babies for whom we had baseline data available (see Appendix 15, Table 76). Excluded babies were significantly less likely to be in surgical NICUs. Eighteen NICUs participated in the PREVAIL trial; however, only 16 were included in our analysis, as one NICU did not consent to linkage of its data and one was excluded because the corresponding laboratory was a poor reporter during the PREVAIL trial period.

Generalisability and applicability

Peripherally inserted central venous catheters were used for at least 1 day in 8443 admissions involving 8206 babies receiving intensive and high-dependency care during the PREVAIL trial period (August 2015 to January 2017) (see Appendix 25, Figure 35).

Comparing rates of bloodstream infection during the PREVAIL trial in PREVAIL and non-PREVAIL babies

Crude and risk-adjusted rates of BSI per 1000 PICC days were similar in PREVAIL babies compared with non-PREVAIL babies in the PREVAIL trial NICUs and babies in non-PREVAIL trial NICUs (Figure 11) (see Appendix 23, Table 83 and Figure 27). BSI rates were lower in LNUs; however, the difference between babies in LNUs and babies enrolled in the PREVAIL trial was not significant. The risk factors included in the risk-adjusted model were gestational age at birth, age at fist PICC, and days of invasive and non-invasive ventilation. Full details of model-building are presented in Appendix 16, Table 77.

FIGURE 11.

Crude and risk-adjusted rates of BSI (for all organisms) per 1000 PICC days in babies who received S-PICCs in NICUs and LNUs, according to enrolment in the PREVAIL trial during the PREVAIL trial period. Adjusted for gestational age at birth, age at first PICC, and days of invasive and non-invasive ventilation. p-value for effect of group (PREVAIL babies in NICU, babies in non-PREVAIL trial NICUs, babies in LNUs) on BSI rate in comparison to babies in the PREVAIL trial. Period for NICUs that participated in the PREVAIL trial depends on NICU start and end date of recruitment; period for other NICUs and LNUs is August 2015 to January 2017 (whole PREVAIL trial recruitment period).

Changes over time in bloodstream infection rates in PREVAIL and non-PREVAIL trial neonatal intensive care units and local neonatal units

From March 2010 to June 2017, there were 55,058 admissions involving 47,669 babies who received PICCs (see Appendix 25, Figure 36). There was no significant change in the risk-adjusted rates of BSI per 1000 PICC days in PREVAIL trial NICUs, non-PREVAIL trial NICUs or LNUs (Table 23 and Figure 12). The trend in non-PREVAIL trial NICUs was not significantly different at the 5% level from the trend in PREVAIL trial NICUs or LNUs. The selected model adjusted for gestational age at birth and days of invasive and non-invasive ventilation (see Appendix 17, Table 78).

TABLE 23 - The unadjusted and risk-adjusted annual percentage change in rate of BSI (clearly pathogenic organisms) during PICC days at risk per 1000 PICC days in PREVAIL trial NICUs, non-PREVAIL trial NICUs and LNUs from March 2010 to June 2017

p-value comparing trend with that of PREVAIL trial NICUs.

Adjusted for gestational age at birth and days of invasive and non-invasive ventilation.

Clearly pathogenic BSI per 1000 PICC days	PREVAIL trial NICUs (n = 16)	Non-PREVAIL trial NICUs (n = 28)	LNUs (n = 68)
Babies (n)	14,667	21,267	15,594
Admissions (n)	15,927	23,537	14,892
Number of PICC days	195,360	296,824	121,750
Number of BSIs	495	736	211
Unadjusted
BSI rate (95% CI)	2.53 (2.31 to 2.76)	2.48 (2.30 to 2.66)	1.73 (1.50 to 1.97)
Annual percentage change (95% CI)	2.33% (–1.98% to 6.82%)	2.14% (–1.32% to 5.72%)	–5.14% (–11.10% to 1.22%)
p-valuea		0.972	0.093
Risk-adjustedb
BSI rate (95% CI)	2.50 (2.28 to 2.72)	2.44 (2.26 to 2.62)	1.64 (1.41 to 1.87)
Annual percentage change (95% CI)	2.73% (–1.62% to 7.27%)	2.63% (–0.86% to 6.25%)	–2.19% (–8.37% to 4.40%)
p-valuea		0.969	0.202

FIGURE 12.

Risk-adjusted rate of BSI (clearly pathogenic organisms) during PICC days at risk per 1000 PICC days, by year of admission in PREVAIL trial NICUs, non-PREVAIL trial NICUs and LNUs. Adjusted for gestational age at birth and days of invasive and non-invasive ventilation. Shading denotes the period of enrolment in the PREVAIL trial.

Trends in rates of bloodstream infection in all babies admitted to neonatal intensive care units and local neonatal units

Changes over time in total late-onset bloodstream infection

From March 2010 to June 2017, there were 161,117 admissions (see Appendix 25, Figure 37) who were at least 2 days old or had a PICC inserted on their day of birth; 2.4% (3798) of these admissions had at least one total late-onset BSI caused by clearly pathogenic organisms. The overall rate was 2.3 (4170/1,849,611) per 1000 days of intensive and high-dependency care.

Risk-adjusted rates of total late-onset BSI (clearly pathogenic organisms) per 1000 days of intensive and high-dependency care remained stable in PREVAIL and non-PREVAIL trial NICUs, but decreased in LNUs (Table 24 and Figure 13). These rates were adjusted for gestational age at birth and days of invasive and non-invasive ventilation (see Appendix 18, Table 79). Risk-adjusted, total late-onset BSI rates per 100 admissions (clearly pathogenic organisms) declined significantly in PREVAIL trial NICUs and LNUs (Table 24 and Figure 14). These rates were adjusted for gestation and for days of invasive and non-invasive ventilation (see Appendix 19, Table 80).

TABLE 24 - The annual change in the rate of late-onset BSI (pathogens) per 1000 days of intensive and high-dependency care and per 100 admissions in PREVAIL trial NICUs, non-PREVAIL trial NICUs and LNUs from March 2010 to June 2017

p-value comparing trend with that of PREVAIL trial NICUs.

Adjusted for gestational age at birth and for days of invasive and non-invasive ventilation.

Only one BSI counted per admission.

Total late-onset BSI	PREVAIL trial NICUs (n = 16)	Non-PREVAIL trial NICUs (n = 28)	LNUs (n = 68)
Babies (n)	37,497	53,967	58,320
Admissions (n)	40,787	58,845	61,485
Number of days	558,303	813,776	477,532
Number of BSIs	1329	1791	1050
Number of admissions with BSI	1190	1612	996
Total late-onset BSI per 1000 intensive and high-dependency care days
Unadjusted
BSI rate (95% CI)	2.38 (2.25 to 2.51)	2.20 (2.10 to 2.30)	2.20 (2.07 to 2.33)
Annual percentage change (95% CI)	–1.87% (–4.46% to 0.80%)	1.68% (–0.58% to 3.99%)	–4.44% (–7.21% to –1.59%)
p-valuea		0.036	0.233
Risk-adjustedb
BSI rate (95% CI)	2.30 (2.18 to 2.43)	2.18 (2.08 to 2.28)	2.11 (1.98 to 2.24)
Annual percentage change (95% CI)	–1.40% (–4.01% to 1.29%)	2.20% (–0.07% to 4.52%)	–2.91% (–5.73% to 0.00%)
p-valuea		0.035	0.342
Total late-onset BSI per 100 admissionsc
Unadjusted
Total late-onset BSI per 100 admissions (95% CI)	2.92 (2.75 to 3.08)	2.74 (2.61 to 2.87)	1.62 (1.52 to 1.72)
Annual percentage change (95% CI)	–4.84% (–7.48% to –2.12%)	–0.60% (–2.90% to 1.75%)	–7.12% (–9.88% to –4.28%)
p-valuea		0.015	0.565
Risk-adjustedb
Total late-onset BSI per 100 admissions (95% CI)	2.83 (2.67 to 2.99)	2.66 (2.53 to 2.79)	1.56 (1.46 to 1.65)
Annual percentage change (95% CI)	–2.86% (–5.57% to –0.08%)	1.44% (–0.93% to 3.86%)	–3.28% (–6.16% to –0.32%)
p-valuea		0.015	0.774

FIGURE 13.

Risk-adjusted rate of total late-onset BSI (pathogens) per 1000 intensive and high-dependency care days of stay, by year of admission in PREVAIL trial NICUs, non-PREVAIL trial NICUs and LNUs. Rates are adjusted for gestational age at birth and for days of invasive and non-invasive ventilation.

FIGURE 14.

Risk-adjusted rate of late-onset BSI (pathogens) per 100 admissions, by year of admission in PREVAIL trial NICUs, non-PREVAIL trial NICUs and LNUs. Rates are adjusted for gestational age at birth and for days of invasive and non-invasive ventilation; only the first BSI per admission was included.

Rates of total late-onset BSI per 100 admissions were lower in LNUs than in NICUs, whereas rates of total late-onset BSI per 1000 days of intensive and high-dependency care were similar. This discrepancy shows that the denominator has an important effect on rates and on trends. In this example, Table 24 shows a similar number of admissions in LNUs and non-PREVAIL trial NICUs, but LNU admissions were shorter, with fewer days of intensive and high-dependency care (477,532 in LNUs, compared with 813,776 in NICUs) (see Table 24).

The contribution of peripherally inserted central venous catheters to total bloodstream infection rates

There was a total of 2476 BSIs in 40,008 admissions receiving intensive and high-dependency care in NICUs and LNUs during the PREVAIL trial recruitment and follow-up period (August 2015 to June 2017): 18% (456) were early onset (no PICC), 46% (1143) were late onset during PICC days at risk, and the remaining 35% (877) were late onset (no PICC) (Table 25). Early-onset BSI was the most frequent type of BSI in babies born at ≥ 32 weeks’ gestation, whereas BSI during PICC days at risk was most frequent in babies born before 32 weeks’ gestation.

Clinical effectiveness randomised controlled trial

We found no evidence of benefit or harm from rifampicin- and miconazole-impregnated PICCs in babies receiving intensive or high-dependency neonatal care. The 95% CI for the primary outcome excluded a 27% reduction or 67% increase in the time to BSI associated with using an AM-PICC, compared with using a S-PICC. Sensitivity analyses did not change these results. We found no differences in mortality at 6 months, or in clinical outcomes recorded at discharge home from the NNU.

Economic analysis

Preterm babies in the PREVAIL trial had an average hospital cost of approximately £84,000 over 6 months, mostly related to critical care in the neonatal care unit. The economic model predicted that preventing BSI is both beneficial, as it generates QALY gains, and cost-saving. As AM-PICCs were found in the PREVAIL trial not to prevent BSIs, the model found that AM-PICCs are not cost-effective. At the current price, AM-PICCs would be cost-effective if they achieved a RR reduction of 3% in BSI rate for babies born at < 28 weeks of gestation, or a reduction of 15% for babies born at ≥ 28 weeks of gestation. The largest driver of uncertainty on the costs and health outcomes is whether or not there is any differential effect between AM-PICCs and S-PICCs in preventing BSIs.

Generalisability analysis

The trial findings were generalisable to babies in NICUs in England. This was based on the fact that there were no differences between babies enrolled in the PREVAIL trial and other babies receiving PICCs in NICUs. We found no differences at the 5% level in the distribution of causative organisms isolated from BSI, or in crude and adjusted rates of any BSI per 1000 PICC days. In addition, post hoc trial analyses found no evidence for an interaction between the primary outcome (HR for time to first BSI) and birth before 28 weeks of gestation compared with birth at ≥ 28 weeks of gestation, suggesting that the relative effect observed in the trial could be generalised to babies receiving PICCs, despite varying gestational ages at birth.

We found stable trends in rates over time in BSI per 1000 PICC days (for clearly pathogenic organisms) in PREVAIL trial NICUs, non-PREVAIL trial NICUs and LNUs from 2010 to 2017. The rate of late-onset BSI (for clearly pathogenic organisms) per 100 admissions declined from March 2010 to June 2017 in LNUs and PREVAIL trial NICUs.

Overall, late-onset BSI during PICC days at risk accounted for 46% of BSIs during days of stay for babies admitted to NICUs or LNUs who received intensive or high-dependency care. Corresponding proportions for babies born before and after 32 weeks of gestation were 55% and 26%, respectively. These findings demonstrate that the time when a PICC is present is a high-risk period for BSI; they do not demonstrate that PICCs are necessarily a cause of BSI.

Strengths and limitations

The trial was adequately powered to detect a halving of the BSI risk and included a representative sample of babies receiving PICCs. The trial provides important new evidence for preterm infants born before 32 weeks of gestation, a group at high risk of infection, with frequent use of PICCs, but for whom trial evidence has been lacking. 29,30 The pragmatic design reflected routine practice, as we had no additional sampling, and used a primary outcome that is routinely used to guide antibiotic treatment in neonatal care.

A further strength was the implementation of the trial. Central web-based randomisation ensured allocation concealment and balanced treatment allocation. We achieved near complete follow-up and assessment for the primary outcome, adhered to a prespecified statistical analysis plan for intention-to-treat analyses and halted recruitment once the sample size was achieved. Slightly fewer babies in the antimicrobial arm received the allocated PICC, probably because the randomised PICC had to be inserted within 48 hours, thereafter the standard PICC was used. The sample size and statistical analysis methods were based on the proportional hazards assumption, which was reasonably upheld.

One limitation was that the intervention was open label, so clinicians could distinguish the type of PICC. We found a slightly increased rate of blood culture sampling in the antimicrobial arm, but the proportions of babies with at least one sample or any PICC tip culture were similar and there were no differences in the timing of PICC removal between trial arms. A further limitation was the lack of power to detect significant differences in rifampicin-resistant organisms isolated from blood or CSF cultures. The small number of resistant organisms was due to few positive cultures, and because only 44–54% of these cultures were tested for rifampicin resistance. The risk of rifampicin resistance in isolates from positive blood or CSF cultures did not differ between trial arms, but was significantly increased in positive tip cultures from AM-PICCs. Selection of rifampicin-resistant Gram-positive bacteria during treatment, when rifampicin is used as the sole antibacterial agent, is well recognised. 113 Testing for resistant organisms was considered by the investigators, the TSC and the IDSMC, but the resistance results were not monitored as the risk of AEs arising was viewed as being low because the limited release of rifampicin from the catheter surface would be unlikely to affect bacteria at any site other than the catheter itself. Even if rifampicin-resistant Gram-positive bacteria did cause infection in an individual patient, routine antibiotic use would be unaffected because rifampicin is rarely used for treatment in the neonatal setting.

Findings in context

The finding that rifampicin- and miconazole-impregnation did not reduce BSI is consistent with other studies (see Table 1). 1,30,36,37 In contrast, RCTs of the effectiveness of minocycline- and rifampicin-impregnated CVCs versus standard CVCs have reported substantial reductions in catheter-related BSIs and, in one trial in PICUs, any BSI. 33,34,114 First, these apparent differences in the effectiveness of rifampicin–miconazole and minocycline–rifampicin impregnation may reflect true differences in antibacterial effects. Miconazole is used to prevent invasive fungal infection in preterm babies, but has the disadvantage that rifampicin is then the sole antibacterial agent when combined with miconazole. Rifampicin is more active against Gram-positive than against Gram-negative bacteria and has synergistic action against staphylococci when combined with another antibacterial such as minocycline, especially against meticillin-resistant strains. 113,115

Second, it is possible that, although minocycline–rifampicin is the most effective type of antimicrobial impregnation in systematic reviews,32,35 this type of impregnation might not effectively reduce overall rates of BSI or sepsis. 116 Trials in adults show beneficial effects of antimicrobial impregnation for catheter-related BSI, but few trials measure the effect on any BSI. Catheter-related infection requires the same isolates from blood and CVC tip and could be biased because of inhibition of positive tip cultures by leaching of antimicrobial from the tip during plating-out for culture. Only the large CATCH trial used any clinically indicated BSI as the primary outcome and found a 57% reduction in time to infection (see Table 1)34,38 Third, the reductions in infection rates in NNUs associated with improved catheter asepsis practices and shorter duration of PICC use may have narrowed the potential for further benefits from antimicrobial impregnation. 47 It is also possible that PICCs are not an independent risk factor for infection in sick preterm babies because of the babies’ high susceptibility to infection from multiple sources, including numerous invasive procedures and devices, gut permeability and immune immaturity. 117

Practice context

Since 2012, the Premistar PICC has been the only AM-PICC available for preterm babies in Europe. Its use has been reported in Germany and Italy,30 but use in the UK was limited to the PREVAIL trial. We are not aware of adoption of the AM-PICC by any UK NNUs outside the context of the trial.

Strengths and limitations

The aim of the economic evaluation was to inform the decision of whether or not the NHS should purchase AM-PICCs rather than S-PICCs for preterm babies in NNUs. The specific objectives were to estimate the hospital costs of the PREVAIL babies over the time horizon of the trial, to determine the cost-effectiveness of AM-PICCs against S-PICCs and the minimum effectiveness of an AM-PICC required to make it cost-effective, and to assess the value of future research.

The use of routine health-care data to estimate the hospital costs of the PREVAIL babies was a strength of the economic evaluation. The economic evaluation secured access to the routine databases that record admissions to NNUs and to PICUs, hospitalisations involving procedures, outpatient appointments and visits to the A&E department. Accessing data from all these routine databases ensured that the estimation of hospital costs was as thorough as possible. It maximised the accuracy of the data on hospital use by avoiding recall bias and by having access to data on the resources involved with each hospitalisation. Furthermore, using routine health-care data precluded asking the parents and guardians to fill in lengthy questionnaires on the number and duration of hospitalisations at a time of personal distress.

A key strength of the economic evaluation was the development of a new decision-analytic model to predict the quality-adjusted life expectancy and NHS costs of using AM-PICCs or S-PICCs over the babies’ expected lifetimes. The model synthesised the most up-to-date estimates of costs and outcomes of BSI in infants in the neonatal care unit, informed by data from the PREVAIL trial linked to routine health-care databases, and from the published literature. The model also considered the different risks associated with gestational age. 118 Although the model was developed to compare PICC types, it can be used to evaluate any interventions to prevent BSI in babies by estimating the minimal reduction in the risk of BSI that is required so that an intervention could be considered cost-effective, and the relationship between minimal risk reduction and maximum price difference.

A further strength is the use of the economic model to estimate the VoI from future research. Specifically, the VoI analysis quantified the magnitude of the health losses following a wrong adoption decision due to parameter uncertainty, the maximum bound of investment that should be warranted to resolve this uncertainty and the key uncertain parameters for which resolving uncertainty will provide the greatest reduction in the risk of making suboptimal decisions.

There were several limitations to the economic analysis. First, it was not possible to estimate the causal effect of BSI and death on hospital costs over 6 months from PICC insertion, and the causal effect of BSI on the risk of death at 6 months. This was because of the lack of difference between PICC groups (precluding an instrumental variable approach), limited number of events and time constraints (given that the routine health-care data were received 3 months before the project’s deadline). Consequently, the model base case assumes that babies incur the same costs irrespective of BSI or survival status, and assumes that BSI does not cause death at 6 months (although it includes an increased risk of death due to BSI at 2 years). As a consequence, the benefits of preventing BSI may be underestimated.

Second, the model assumes that BSI increases the risk of death and NDI at 2 years of age. The evidence of this causal link was based on the published literature, which, given the enormity of the potential evidence base, was identified from a citation search rather than from a systematic review, which would have been outside the scope and timeline of the project. As a consequence, there is a risk of having omitted some studies in the final evidence review and meta-analysis. Nonetheless, the starting point for the citation search (the so-called ‘pearls’) was informed by the PREVAIL trial clinical team, and great care was taken in matching the outcomes identified in the literature review with those collected in the trial. Moreover, the citation search identified three systematic reviews and one umbrella review, published between 2013 and 2016,78–80,119 thereby providing some reassurance that most, if not all, of the relevant studies were included. The literature on the link of BSI to death and NDI is necessarily observational, and scarce. If this link is not causal, or if it is smaller in magnitude, the value of preventing BSI may have been overestimated. Therefore, the minimum risk reduction for interventions, such as an AM-PICC, to be cost-effective may have been underestimated. This structural uncertainty was explored in the scenario analysis, but was not considered in the VoI framework. This means that the value of future research in the effectiveness of interventions to prevent BSI may have been overestimated, compared with the value of future research on the causes of NDI and death in early years.

Third, the model structure constrains the impact of preventing BSI in increasing the risk of NDI and death at 2 years of age. There are some studies suggesting that antibiotics, given to treat infection, increase the risk of NEC, which would, in turn, increase the risk of NDI. 25,26,120 However, no studies were identified that enable the direct effect of BSI on NDI to be disentangled from the indirect effect via antibiotic treatment; hence, the model structure excludes NEC. If NEC was confirmed to play a role in the pathway leading to NDI over and above the direct effect of BSI, and if BSI causes NEC, preventing BSI may be more cost-effective than this study suggests. Conversely, if NEC is on the causal pathway for NDI and death at 2 years, but it is unrelated to BSI, preventing BSI will be less cost-effective.

A fourth limitation was restriction to the perspective of NHS hospitals for costs during the 6-month follow-up period. Ideally, the model would include all the costs falling on the NHS, including not only hospital costs, but also costs of community health care. This was not possible because there are no routine health-care databases that compile the use of community health-care services. Furthermore, at project conception, it was deemed excessively burdensome to ask parents for details of their use of community health-care services. Nevertheless, the lack of data on community health-care costs is unlikely to have a large impact on the results, given the high costs related to hospitalisations. Costs falling on other sectors, such as social care and education, are likely to be relevant. However, their inclusion would represent a departure from the NHS perspective and would require the consideration of how to account for costs falling on different sectors. 121

Fifth, the model was also restricted to health benefits for the child, by considering the impact of BSI on death and NDI, and its consequences on the babies’ length of life and HRQoL. Children’s health may have spillover effects on their parents. 122,123 Therefore, avoiding BSI may have beneficial consequences to parents’ HRQoL. If this is the case, the benefits in terms of QALYs for parent and child of preventing BSI may have been underestimated and the magnitude of the necessary risk reduction for interventions to be cost-effective may have been overestimated.

A sixth limitation relates to the measure of NDI, which was retained from the previous model of Mangham et al. 71 It is relatively crude and might have been superseded by more recent advances in paediatrics. As far as model results are concerned, most babies are classified as having no impairment at 2 years of age. However, less evident cognitive or motor deficits might become apparent at school age, even in this group, causing additional burden in terms of both health-related and education costs, and QALYs lost. Again, if this is the case, the model will underestimate the benefits from preventing these additional minor deficits related to the occurrence of BSI, which, if accounted for, would further increase the cost-effectiveness of interventions to prevent it.

Using routine health-care data to estimate hospital costs had some limitations. Given that linkage of the PREVAIL babies’ data was conducted by the data providers, there was limited information on the reasons for missing data. Furthermore, as the costing of hospital care is based on HRGs, hospitalisations with insufficient data to derive a HRG were discarded. Nonetheless, complete data were retrieved for most PREVAIL babies. Moreover, any missing data are likely to be related to errors in data entry at the hospital level, which are unlikely to be related to the babies’ characteristics and their hospital care, and hence can be assumed to be missing completely at random. Another limitation was the inconsistencies in the dates in some records, which were needed to calculate the hospital length of stay. However, for the estimation of hospital costs, the dates of hospitalisations are used only to select the hospital care within the trial follow-up period of 6 months. Therefore, the approach taken to analyse the dates is unlikely to have a large impact on the results.

Findings in context

We found no published economic analyses that compared PICC impregnation in newborn babies. Previous cost-effectiveness studies for impregnated PICCs were in older populations and used different antimicrobials for impregnation, precluding meaningful comparisons. 124–127

A previous study71 estimated the health outcomes and costs of care of preterm babies, but it did not assess the cost-effectiveness of interventions to improve outcomes of preterm babies. The results of Mangham et al. 71 are similar to the results of the present study under the standard care (S-PICC) policy, even though some of the model inputs are different. Mangham et al. 71 predicted that at 18 years of age 36% of babies born at gestational age 23–27 weeks (66% of babies born at gestational age 28–32 weeks) would have no NDI, 10% born at gestational age 23–27 weeks (17% born at gestational age 28–32 weeks) would have mild NDI, 5% born at gestational age 23–27 weeks (6% born at gestational age 28–32 weeks) would have moderate NDI and 4% born at gestational age 23–27 weeks (4% born at gestational age 28–32 weeks) would have severe NDI. In the present study, the model predicted that, under the current policy of using S-PICCs, 45% of babies born at gestational age 23–27 weeks (67% of babies born at gestational age 28–32 weeks) would have no NDI, 17% born at gestational age 23–27 weeks (20% born at gestational age 28–32 weeks) would have mild NDI, 9% born at gestational age 23–27 weeks (6% born at gestational age 28–32 weeks) would have moderate NDI and 7% born at gestational age 23–27 weeks (3% born at gestational age 28–32 weeks) would have severe NDI. For babies born at < 28 weeks’ gestation, the Mangham et al. 71 model estimates the total average cost per survivor to 18 years at £136,790 (95% CI £50,222 to £261,873), compared with an average lifetime cost per baby (using S-PICCs) predicted in our model of £126,168 (95% CI £120,133 to £132,655).

Results from the economic analysis show that the RR of BSI is the main contributor to overall parameter and decision uncertainty. If BSI in infancy increases the risk of NDI and death, as suggested by observational studies and included in the model, interventions that prevent such BSI offer a large potential for cost-effectiveness, even if their efficacy is small. 10,74,78 Therefore, future applied research should focus on the evaluation of the effectiveness of interventions to prevent BSIs. However, the increase in risk of NDI and death reported by observational studies may not be a true reflection of the effect of BSI. It is possible that there is some residual confounding, in that babies who have poorer health are more likely to suffer a BSI, as well as being more likely to have NDI or die. If this is the case, the association between BSI and NDI/death may be overestimated, thereby leading the cost-effectiveness model to overestimate the benefits of preventing BSI in the long term. For these reasons, more research is needed on the effect of BSI on long-term health outcomes.

Reflecting the structural uncertainty on the link between BSI, NDI and death is a key challenge. The methodological literature is unclear about how to reflect structural uncertainty from observational studies, although some approaches have been proposed in the past. 128 Further research is warranted to develop adequate methods that are able to incorporate and assess potential biases due to the inclusion of observational evidence, both directly (i.e. in the model structure) and indirectly (i.e. in the evidence synthesis process). In this respect, clinical research could help inform future models, for example via longitudinal studies following preterm babies over time. These would record various types of data, including linkage to hospitalisation, community and primary care data for health outcomes, and measures relevant to health captured in non-health data, for example cognitive function measured through school achievement trajectories, so that causal estimates of the impact of infection could be estimated.

Strengths and limitations

A key strength of our study is the national coverage of 92% of NICUs and LNUs across the NHS in England over 7 years; this minimised referral biases, provided a large enough sample to evaluate subgroups and used routinely submitted laboratory reports, thereby minimising clinician response bias. Our data on BSI are laboratory confirmed and we have data on the organism cultured and dates from both infection surveillance and clinical records, which enables us to tailor specific definitions of BSI.

Limitations include a lack of precise timing of culture sampling (day rather than hour), no consent to use data from 12 units, and lack of full data for 162 PREVAIL trial participants. Furthermore, the presence of a PICC was not recorded in 6% of PREVAIL babies known to have a PICC from trial CRFs. It is unlikely that these errors are limited to PREVAIL babies; hence, some PREVAIL and non-PREVAIL babies were misclassified as not having a PICC.

A further limitation is linkage error, which can have an important impact on trend analyses. In our study, linkage error arises predominantly from missed links, and, to a lesser extent, from false links due to incorrect or missing identifiers. In the linked data, the BSI rate in PREVAIL babies randomised to receive a S-PICC was 8.1 per 1000 PICC days, compared with 10.6 in the PREVAIL trial, highlighting the underestimation of our results. This is probably a result of missed links due to incomplete identifiers or under-reporting to the infection surveillance system. The quality and completeness of identifiers improved in both data sets (NNRD and infection surveillance) over time. This improvement could have led to a spurious increase in BSI rates. Therefore, we need to be cautious in interpreting the stable, increasing and declining BSI rates. Further research is needed to understand the case mix, practice and service factors affecting changing rates of BSI over time, taking into account all periods at risk throughout neonatal care. Stable rates in NICUs may reflect a combination of better infection control, allowing use of PICCs in more high-risk periods. For example, when PICCs are used for shorter durations, it is likely that the PICCs are used during higher-risk periods, such as during stabilisation after birth. We would expect rates of BSI per 1000 PICC days to be higher during shorter, but higher-risk, periods, even though overall BSI risk during NNU stay would decrease. Similarly, replacement of umbilical venous catheters with PICCs may decrease BSI rates if all catheter days were counted. However, the rate of BSI per 1000 PICC days would increase because BSIs that were previously counted during umbilical venous catheter days would be counted while a PICC is in situ.

Findings in context

The total rate of BSI (clearly pathogenic organisms) of 2.4 per 100 admissions was slightly higher than the rate of 1.8 per 100 admissions reported in a retrospective cohort study of 34 NICUs and LNUs in the UK from 2005 to 2014. 12 This may reflect the more stringent definition used in the study of 34 NICUs that required a prescription of at least 5 days of antibiotics, or the reliance on voluntary reporting by clinicians to the study. In addition, we excluded babies who received special care from our study, who would have fewer infections. Excluding special care made the data more comparable between NNUs, and over time, as babies are kept in special care for varying lengths of time; however, this excluded 11.5% of total late-onset BSIs in all NNUs. Our finding of a declining trend in total BSIs per 100 admissions in PREVAIL trial NICUs and LNUs is similar to trends reported in the study of 34 UK NICUs and LNUs. 12

Before-and-after studies have reported reductions in rates of BSI per 1000 PICC days following the introduction of care bundles. 47,48 However, this was not seen in our study. This may be due to the improved ascertainment of BSI over time masking true trends. Alternatively, our study represents all centres across England, where rates may differ from those voluntarily participating in a study. In our study, a mix of decreasing and increasing rates in different NNUs may have resulted in a stable average rate. Furthermore, the BSI rates may have only temporarily decreased, thereby not affecting the long-term trends.

Participants

We would like to thank the 861 babies who participated in the PREVAIL trial, along with their parents and families, for their invaluable contribution to this research.

Trial sites

We are grateful to the PIs and RN teams at each trial site who recruited participants and supported them and their families throughout the trial (in order of number of patients recruited): Bradford Royal Infirmary (Sam J Oddie and Rachel Wane); Leicester Royal Infirmary (Marie Hubbard and Rosalind Astles); Birmingham Women’s Hospital (Andrew Ewer and Rachel Jackson); St Mary’s Hospital, Manchester (Ranganath Ranganna and Nicola Booth); Liverpool Women’s Hospital (Kiran Yajamanyam and Karen Harvey); Homerton University Hospital (Narendra Aladangady and Asha Mathew); The Jessop Wing, Sheffield (Elizabeth Pilling and Pauline Bayliss); Royal Oldham Hospital (Natasha Maddock and Louise Woodhead); The Royal London Hospital (Ajay Sinha and MaySze Chang); Royal Preston Hospital (Sandeep Dharmaraj and Claire Lodge); Queen’s Medical Centre, Nottingham (Jon Dorling and Helen Navarra); John Radcliffe Hospital (Charles Roehr and Sheula Barlow); Royal Bolton Hospital (Mahesh Yadav and Claire Abbott); Leeds General Infirmary (Kathryn Johnson); Nottingham City Hospital (Dushyant Batra and Yvonne Hooton); St Michael’s Hospital, Bristol (Pamela Cairns and Jennifer Chapman); Queen’s Hospital, Romford (Bal Krishnan Sharma and Helen Smith); and Newham General Hospital (Imdad Ali and Ivone Lancoma-Malcolm). We thank the 53 hospital trusts across the UK that agreed to act as continuing care sites for the trial and assisted with collection of important follow-up data when participants were transferred away from their recruiting site.

Liverpool Clinical Trials Centre

We thank the LCTC staff: Zoe Craig, Sue Howlin and Kate Silvera-Cull for their work as data managers on this study; Anna Rosala-Hallas and Elizabeth Conroy who acted as randomising statisticians and produced the randomisation lists; and Ashley Best who undertook quality control checks.

Public engagement

We thank BLISS, a patient advocacy charity for babies born premature or sick, for its support of the trial, assistance with review of public-facing documents and dissemination of results (registered charity number 1002973; www.bliss.org.uk/).

Trial Steering Committee

We thank Mike Sharland (chairperson), Stephanie Chadwick, Edmund Juszczak and Win Tin for their oversight and guidance.

Independent Data and Safety Monitoring Committee

We thank Nicholas Embleton (chairperson), Alison Balfour and Louise Stanton for their oversight and guidance.

Clinical effectiveness randomised controlled trial

The use of HES data was approved by the Health and Social Care Information Centre (now known as NHS Digital) for the purpose of this study (DARS-NIC-73974-P0L1Z-v0.9). HES data © 2018, reused with the permission of the Health and Social Care Information Centre. All rights reserved.

Economic analysis

Electronic patient data recorded at participating NNUs that collectively form the UK Neonatal Collaborative (UKNC) are transmitted to the NDAU to form the NNRD. Laura Bojke, Rita Faria and Alessandro Grosso had full access to all the data in the study and take full responsibility for the integrity of the data and accuracy of the data economic analysis. We are grateful to all the families that agreed to the inclusion of their baby’s data in the NNRD, the health professionals who recorded data and the NDAU team.

The PICANet is commissioned by the Healthcare Quality Improvement Partnership (HQIP) as part of the National Clinical Audit and Patient Outcomes Programme; the Welsh Health Specialised Services; NHS Lothian/National Services Division NHS Scotland; the Royal Belfast Hospital for Sick Children; The National Office of Clinical Audit, Republic of Ireland; and HCA Healthcare UK.

The HQIP is led by a consortium of the Academy of Medical Royal Colleges, the Royal College of Nursing, and National Voices. It aims to improve health outcomes and to promote quality improvement. This publication is based on data collected by or on behalf of the HQIP, which has no responsibility or liability for the accuracy, currency, reliability and/or correctness of this publication.

This research was informed by data collected by NHS Digital (formerly the Health and Social Care Information Centre), © 2015–18, the Health and Social Care Information Centre. Re-used with the permission of the Health and Social Care Information Centre. All rights reserved.

Generalisability analysis

Electronic patient data recorded at participating NNUs that collectively form the UKNC are transmitted to the NDAU to form the NNRD. Ruth Gilbert, Katie Harron and Caroline Fraser had full access to all the data in the study and take full responsibility for the integrity of the data and accuracy of the data analysis. We are grateful to all the families that agreed to the inclusion of their baby’s data in the NNRD, the health professionals who recorded data, and Professor Neena Modi and the team at the NDAU. National infection surveillance data from the Second Generation Surveillance System was provided by PHE.

Data sources

The economic analysis conducted by the team at the UoY for the PREVAIL project required routinely collected health-care data from NHS Digital, PICANet and NDAU, as well as data collected in the clinical trial by the UoL. The team at UCL developed the algorithm to select the babies enrolled in the PREVAIL trial who were recorded in the NNRD held by NDAU.

Data flows

The data flow was as follows: the UoL sent the patient identifiers to NHS Digital, PICANet, NDAU and UCL. NHS Digital selected the cohort using the identifiers and sent the administrative data identified with trial identifier to the UoY; the process was similar with PICANet, but the data were sent to the UoL, then the UoY. The UoY generated a database with the NHS Digital data on date of death and sent it to UoL. UCL linked the PREVAIL trial cohort to NNRD as part of the PREVAIL trial generalisability analysis and sent Badger identifiers (IDs) (a pseudonymised identifier) for PREVAIL babies to NDAU; NDAU used the Badger IDs to select the cohort and sent the data to the UoY. UoL sent the PREVAIL trial data to the UoY.

Data transfer

The UoY submitted the data-sharing applications to NHS Digital, PICANet and NDAU on 21 November 2016. The UoY received the NHS Digital data on hospitalisations on 24 May 2018, and the NHS Digital data on date of death on 27 September 2018, the PICANet data on the 9 May 2018 and the NDAU data on 24 August 2018. The UoY initiated the process to develop the data-sharing agreement between the UoY and the UoL on 3 May 2018. The UoY received the data on the 16 August 2018.

Preparing the data-sharing application

The UoY submitted the data-sharing application to NHS Digital on 21 November 2016.

Revising the data-sharing application

NHS Digital had a number of queries with the application, which had to be addressed before formal submission to the Independent Group Advising on the Release of Data (IGARD). These issues were related to ensuring that the project had informed consent for sharing of date of death; ensuring that the trial participants had access to information about how their data were being used; processes for withdrawal from the data-sharing process; explaining the rationale for the project in lay terms; and detailing the benefits to the NHS, outputs and target dates of conducting the research. This took place between November 2016 and September 2017.

Meeting the security requirements

The data-sharing application for NHS Digital required answering various information technology queries from the NHS Digital by the UoY and the UoL. This took place between May and July 2017.

Submission to the Independent Group Advising on the Release of Data

The data-sharing application was submitted to the IGARD on 11 September 2017.

Update to the framework contract

The IGARD approved the application on 20 September 2017. At this point, it emerged that the UoY and UoL had not yet signed up to the the Data Sharing Framework Contract version 2. This meant that the data-sharing agreement could not be issued until the two institutions signed up to it, which took place in October.

Signing the data-sharing agreement

In December 2017, the UoY contracts’ office concluded that UCL and UoL had to sign the hard copies of the data-sharing agreement so that UoY could sign it electronically. UCL signed it on 2 January 2018 and UoL on 5 February 2018. The data-sharing agreement was executed on 27 February 2018.

Transfer of hospitalisation data

The data were received at the UoY on 24 May 2018.

Date of death missing

On 6 June 2018, the UoY contacted NHS Digital to enquire about the data on date of death, which were missing from the data sets, but were included in the data-sharing agreement. On 27 September 2018, NHS Digital confirmed that the data were ready for transfer.

Transfer of date of death data

The data were received at Centre for Health Economics on 27 September 2018.

Transfer of the date of death to University of Liverpool

On 24 October 2018, the UoL confirmed that it still required the date of death data; the data were transferred by the UoY on the same day.

Data-sharing application to the Paediatric Intensive Care Audit Network

The UoY submitted the data-sharing application to PICANet on 21 November 2016. PICANet replied on 22 November, explaining that data-sharing applications were now processed via HQIP, which required another data-sharing application and agreement forms.

Data-sharing application to the Healthcare Quality Improvement Partnership

The UoY developed the data-sharing application and agreement between 29 November 2016 and 2 March 2018.

Approval from the Healthcare Quality Improvement Partnership

The UoY submitted the data-sharing application and agreement to HQIP on 14 March 2017. HQIP approved the application on 16 June 2017. PICANet signed the agreement on 16 June, and HQIP signed on 19 July 2017.

Data transfer

The UoL transferred PREVAIL trial identifiers to PICANet on 5 March 2018. The UoY received the data on 9 May 2018.

Data-sharing application

The UoY submitted the data-sharing application to NDAU on 21 November 2016. NDAU approved the data-sharing application on 5 May 2017.

Data-sharing contract

The UoY contacted NDAU for the data-sharing contract on 29 June 2017. The data-sharing contract was signed on 10 January 2018.

Data-sharing agreement

On 7 March 2018, NDAU requested a data-sharing agreement in addition to the contract. The UoY signed the data-sharing agreement on 19 March 2018.

New data-sharing agreement

On 23 May 2018, NDAU informed the UoY that, given that the General Data Protection Regulation (GDPR)132 had already come into force, it required a new data-sharing agreement that was GDPR compliant. On 26 June 2018, NDAU concluded that, rather than a new data-sharing agreement, an amendment to the original contract, which had been signed on 10 January 2018, was needed. The addendum to the original contract was executed on 24 August 2018.

Privacy notice

University College London, as the study sponsor, is required to approve the privacy notice. The UoY sent the privacy notice to UCL for approval on 10 July 2018. It was approved on 13 August 2018.

Data transfer

The UoY received the data on 24 August 2018.

Developing the data-sharing agreement

It came to light in early May 2018 that the UoY needed to have an agreement in place with the UoL to receive the PREVAIL trial data, given that the project was contracted separately between UCL and each of the partner organisations. The UoY initiated the data-sharing agreement between the UoY and the UoL on 3 May 2018.

Sign-off by University of Liverpool

The UoL signed off the agreement on 4 July 2018.

Sign-off by sponsor

University College London was contacted on 7 July 2018 to sign off the data-sharing agreement and privacy notice (see Privacy notice). UCL commented on the data-sharing agreement on 1 August 2018.

Execution of contract between all parties

On 16 August 2018, the contract was fully executed.

Data transfer

The UoY received the PREVAIL trial data on 16 August 2018.

Cleaning prior to deriving Healthcare Resource Groups

As discussed in Chapter 4, Costing hospital care, hospital care was costed based on the HRGs. The HES data sets, that is HES APC, HES outpatient and HRS A&E, did not include the costing HRGs. Therefore, the hospital care recorded in the HES data sets was passed through the HRG grouper software to derive them.

Before being passed through the grouper software, the HES data sets were cleaned to ensure both internal consistency and to fulfil the grouper software requirements. It was essential to ensure that dates were chronologically sound (e.g. episode start happening before episode end, admission date happening before discharge date, admission date happening before or on episode start date), that poorly coded observations (e.g. record identifier, episode duration, episode end date missing) and duplicates (in particular, episodes sharing the same identifier) were dropped, and that diagnosis and procedure codes included only alphanumeric characters. Episodes sharing the same episode order identifier as at least one other episode in the same spell, but showing an unspecified diagnosis code (‘R69X6’), needed to be dropped. The grouper does not distinguish these particular episodes from the other correct episodes in the same spell and will not generate a HRG for any episode of that spell. Therefore, the data set was first sorted using trial identifier, NHS provider code and relevant dates, and then episodes showing a primary diagnosis code of ‘R69X6’, and sharing the same NHS provider code and episode order identifier of the immediately adjacent episode (above or below) in the data set, were dropped.

Cleaning prior to costing

The data sets required additional cleaning before costing the HRG. Figures 20 and 21 summarise the process.

FIGURE 20.

Preparation of the HES APC data (received from NHS Digital).

FIGURE 21.

Preparation of the HES outpatient and A&E data (received from NHS Digital).

First, it was necessary to create an indicator variable for the type of episode (elective vs. non-elective, long vs. short stay) so that the appropriate unit cost would be attached to its respective HRG. Episodes for which there was not enough information to declare the episode type were dropped from the data set.

Some of the HRG codes were different between the 2016/17134 and the 2015/16 reference costs. 62 Therefore, the ‘new’ codes were replaced with their older counterpart before attaching the reference cost table to the HRG codes (Table 41).

A small number of HRG codes were introduced in 2016/17 and did not have a corresponding code in the previous year’s schedule. They were therefore deflated to 2015/16 prices using the Hospital and Community Health Service index (Table 42). 135

Two pieces of information were required to correctly identify the HRG for the A&E data set: the type of department and whether or not patients were admitted for subsequent investigations (Reference Cost Guidance, section 769). It was assumed that all babies were admitted to a ‘Type 01’ structure, representing hospital emergency departments.

In case an A&E admission was linked to a subsequent inpatient admission, the A&E data set presents the unique APC episode identifier. Therefore, a non-missing APC episode identifier was taken as the signal that that A&E admission led to a subsequent inpatient admission, in order to fulfil the second criteria for the correct unit cost identification.

Methods

Methods

Analysis

The analysis was initially descriptive on:

• The number of babies who had a clinically serious BSI with S-PICCs by gestational age subgroup, which represents the probability of infection with a S-PICC in the model.

• The number of babies who died over the time horizon of 6 months, taking death as recorded either in the PREVAIL trial CRFs or in the HES records via the Patient Demographics Service, by gestational age subgroup. This represents the probability of death irrespective of the type of PICC and irrespective of prior clinically serious infection.

In a second stage, a regression analysis was conducted on the probability of death given gestational age subgroup and prior clinically serious infection. The regression analysis explored the impact of using generalised linear models with binomial family or Poisson family and log link.

Results

Tables 57 and 58 show the results of the descriptive analysis. The probability of having a clinically serious BSI with a S-PICC was 14.52% (95% CI 9.79% to 20.41%) in the younger gestational age subgroup and was 3.80% (95% CI 1.54% to 7.68%) in the older gestational age subgroup. The probability of death over the time horizon of 6 months is shown in Table 58.

Table 59 shows the results of the regression analysis of the probability of death given gestational age and prior clinically serious BSI. The best-fitting regression is the regression including both explanatory variables. It suggests that having a clinically serious BSI is associated with 78.4% greater risk of death (RR 1.784), and that being born at a gestational age of 28–32 weeks is associated with an 85.5% lower risk of death (RR 0.245).

It is not clear whether this is a correlation or a causal association. There may be other factors that increase the risk of clinically serious BSI and increase the risk of death, for example other health problems that the babies may have been born with. Without controlling for these other factors, it is not possible to ascertain whether or not preventing clinically serious BSI reduces the risk of death to the extent that the regression analysis suggests. Given the small number of deaths, the regression analysis is constrained in the number of variables that can be included.

Method

The following equations explain the methodology.