The health impacts of energy performance investments in low-income areas: a mixed-methods approach

Health impacts of energy efficiency improvements

It is clear that housing quality is associated with a range of health and psychosocial outcomes. However, most evidence is derived from cross-sectional research. This is problematic, as those living in poor housing are most likely to be socioeconomically deprived and have long-standing illness. The causal pathways between poor housing and poor health can therefore be determined only by intervention studies. In a systematic review of the literature, Thomson et al. 48 identified 39 housing intervention studies that reported quantitative or qualitative data on health and associated socioeconomic outcomes. Of these, 19 evaluated affordable warmth and energy efficiency improvements relevant to modern-day housing conditions (i.e. post 1985), including five randomised controlled trials, five controlled before-and-after studies and five uncontrolled or retrospective studies. Thomson et al. 48 concluded that affordable warmth and energy efficiency measures may produce improvements in general health, respiratory health and mental health, but that interventions targeting at-risk populations (i.e. those with inadequate warmth and pre-existing conditions) are more likely to be successful than general, area-based, programmes.

Two randomised controlled studies conducted in New Zealand by Howden-Chapman et al. 49,50 found that improving energy efficiency through insulation improved respiratory health in both children and adults, and that improved non-polluting heating systems reduced symptoms of pre-existing asthma in children. In the case of asthmatic children, benefits could be linked to the rise in temperature in both the living room and the child’s bedroom as well as lower levels of nitrogen dioxide. 50 In a randomised trial, Barton et al. 51 found substantial reductions in non-asthma-related chest problems and the number of reported asthma symptoms among the intervention group for both adults and children.

Energy efficiency measures also appear to be beneficial for mental health, although studies have shown mixed results. 48 Howden-Chapman et al. 49 found significant improvements in three subscales of the Short Form questionnaire-36 items (SF-36), namely in the ‘happiness’, ‘vitality’ and ‘role emotional’ scales. However, the authors did not report the overall results for the Mental Health Composite Scale (MCS). Barton et al. 51 found no significant differences between the intervention and control groups regarding the mental health subscales of either the SF-36 or the General Health Questionnaire-12 items. Braubach et al. 52 similarly found non-significant differences in self-reported depression between the intervention and control groups. The authors noted that the follow-up questionnaire was distributed within a few months of the intervention, and that detailed analysis of the data had not been undertaken in order to better understand the impacts of both time and socioeconomic variables such as age. Shortt and Rugkåsa53 reported that stress and mental illness increased significantly in the control group but showed a non-significant decrease in the intervention group.

Psychosocial impacts of energy efficiency improvements

Studies examining the impacts of energy efficiency improvement programmes have thus far focused primarily on a limited number of health outcomes. Few large-scale controlled studies have been undertaken to understand the wider psychosocial impacts of such programmes. 48 The predominantly qualitative literature suggests two inter-related pathways that may link energy efficiency investments to better mental and physical health. 54–56 The first pathway is the process in which energy efficiency improvements to homes lead to better thermal living conditions, through improved indoor air temperature and decreased humidity, both of which contribute to reduced damp-related housing problems. 57 Warmer, drier homes can contribute to improved respiratory health, and also better mental health through improved thermal satisfaction,58 expanded living space and reduced social interactions. 59 The second pathway is the process in which energy efficiency measures lead to improved well-being by making heating more affordable. 6 Reduced spending on heating bills alleviates financial stress and fuel poverty among low-income households,60,61 and helps to free financial resources for better food security45,46 and reduced social isolation. 31 Social isolation may reduce further because people may become less reluctant to invite people into their homes with improved internal conditions. 62

Energy efficiency improvements and internal conditions

The evidence of the impact of energy efficiency improvements on indoor conditions is limited. Overall, based on available studies that have been conducted so far, energy efficiency measures produce modest increases in mean indoor air temperatures and small increases in mean humidity levels. 48 The Warm Front study group reported mean living room temperature increases of 0.58 °C for insulation and 1.36 °C for heating measures, and mean bedroom temperature changes of 1.14 °C for insulation and 1.98 °C for heating measures, with greater changes for dwellings that received both heating and insulation measures (1.52 °C and 2.31 °C for living room and bedroom, respectively). 63 Howden-Chapman et al. 49 reported an average increase in bedroom temperature of 0.50 °C and an average decrease in humidity level of 2.3% relative humidity (RH). The Glasgow Warm Homes Study60 reported increases in mean temperatures of > 2 °C in the living room and almost 3 °C in the bedroom, but no significant changes in RH levels.

More recently, there have been suggestions that increasing the energy efficiency of a home could have detrimental effects on people’s health. 64 Reduced ventilation through insulation and draughtproofing may increase RH levels65 and, as a result, promote mould growth. 66,67 Indeed, low ventilation rates and homes with greater energy efficiency are associated with asthma and allergic symptoms in children. 68–70

The evidence on energy efficiency investments and indoor conditions, however, is scant. Most research in the area has been cross-sectional71 and has not included control households,72 spot measurements8 or short-term monitoring. 60 As previously observed by Oreszczyn et al. ,68 most studies did not correct for external conditions during the monitoring periods. Evidence for increases in RH levels has been anecdotal or inferred from cross-sectional studies only. Raising indoor air temperatures through better insulation should reduce RH levels unless there is inadequate ventilation. 64 Overall, based on the available studies that have been conducted to date, it appears that energy efficiency investments produce modest increases in mean indoor air temperatures and small increases in mean humidity levels. 48

Conclusion

The literature review presented here shows that housing improvements that increase the energy efficiency of homes have the potential to improve the health of residents, in particular if they are targeting at-risk populations with inadequate warmth and pre-existing conditions. 48 However, most research involves observational studies using self-completion questionnaires. Field studies that rely on survey methodologies are vulnerable to biases from low response rates, attrition and self-reporting. Anonymous data linkage of routinely collected health data, which is less vulnerable to such biases, has not, to our knowledge, been used before to examine the impact of energy efficiency improvements (see Chapter 2). 73 In addition, less is known about the wider psychosocial impact of energy efficiency improvements. There is a distinct lack of good-quality quantitative evidence regarding the pathways and processes that may contribute to better health in the longer term (see Chapter 3). 54 Moreover, only a limited number of household monitoring studies have been conducted to examine the impacts of energy efficiency improvements on indoor hydrothermal conditions. Research in this area has been marred by a number of methodological and analytical issues and has relied on studies with relatively small sample sizes (see Chapter 4). Finally, economic evaluations have rarely been carried out alongside housing improvement programmes to assess their health-related quality of life and economic impacts. 74 Health economic evaluations are essential to inform policy-makers about the value for money of energy efficiency investments (see Chapter 5).

Study design

The data linkage study consisted of a quasi-experimental analysis of residents living within homes having undergone energy efficiency improvements. The research utilised individual-level health data held within the SAIL databank anonymously linked with property-level intervention data provided by the housing scheme operators. Intervention and comparator groups were created through retrospective analysis of SAIL data from interventions carried out in 2010 and 2011. Health outcomes were obtained for the entire period that residents were present within the homes.

Setting

In the first phase of the intervention programme, a total of £68M was invested, including leveraged funding. The programme had the joint aims of delivering affordable warmth, alleviating fuel poverty, reducing CO₂ (carbon dioxide) emissions and boosting economic development and regeneration in Wales. LAs and registered social landlords (RSLs) submitted project plans to improve the thermal efficiency of homes in Wales. The majority of homes were social homes. Work for 28 schemes was carried out in 2010 and 2011; it covered a wide geographical area across Wales and is referred to as the intervention study group (Figure 1).

FIGURE 1.

Locations (in blue) of (a) the top 10% of deprived areas; and (b) the intervention areas.

Participants

Intervention home addresses and measures were collated and imported into the SAIL databank through a split file method designed to maintain the anonymity of people living in the properties. 83 The first part of the split file containing addresses and unique property reference numbers was sent to a trusted third party, the NWISs, and replaced with a Residential Anonymous Linking Field (RALF). 79,84 The RALFs were securely transferred to the SAIL databank with a further level of encryption added by the SAIL technical team prior to being made available to researchers under controlled data access agreements. The second part of the split file contained intervention data with no identifiable data. This file was issued directly to SAIL and the two files were re-linked in the SAIL databank after removing the address data.

A similar split file method was followed to create anonymous (individual) linking fields (ALFs) for each person in the SAIL databank. 82 The first part of the split file containing identifiable data (including names and dates of birth) was issued to NWIS and replaced with the ALF prior to a further level of encryption added prior to researcher data access. Data relating to health-care utilisation and other administrative data, as supplied to SAIL in the second half of the split file process, was relinked in the SAIL databank, ensuring that anonymity was maintained.

The encrypted property-level (RALF) data is linked to individual-level (ALF) data in the Welsh Demographic Service (WDS) data set, which contains details of every person registered with a general practitioner (GP) in Wales along with their address histories and are based on addresses registered with a GP. We extracted people living within intervention properties according to our study inclusion criteria: a person needed to be resident in the property for ≥ 60 days during the study period (2005–14). People were retained in the study if they were living in the property during the intervention, moved out pre intervention or moved in post intervention. We used multilevel modelling methods that take into account unbalanced data; people did not need to be in the study for both the before and after phases.

Obtaining individual ALFs registered as occupants of the houses in our study allowed us to link to individual-level health data and mortality records without ever seeing personal, identifiable information or low-level geographical information.

The same method was applied for two groups of comparator homes. Social housing addresses from a Welsh LA were provided for the first comparator group. The second comparator group comprised all homes located in the top 10% of deprived lower super output areas (LSOAs) in Wales, based on the 2011 Welsh Index of Multiple Deprivation (WIMD) income domain.

Data sources

Address and intervention data were collected through contacting and requesting standard information from 28 LAs and RSLs. The supplied information was collated into a master data set by researchers at Cardiff University who had no access to SAIL data. This was important to maintain data privacy so the SAIL data analyst did not have access to both the identifiable address data and the anonymised version. The data were subsequently imported into SAIL through a split file method by our trusted third-party supplier, as described previously. The procedure ensured that the anonymity of homes and, thus, residents was maintained. Intervention dates were received in SAIL in a non-standard, non-codified manner. Data cleansing was carried out within the SAIL databank to reformat intervention dates and descriptions with a number of rules applied, described in Participants.

A Welsh LA provided all addresses of their social housing stock, which were transferred into SAIL to form the first comparator group. A second comparator group was created by selecting LSOAs forming the top 10% of deprived areas in Wales from the WIMD 2011 income domain, then linked to homes within the WDS containing addresses based on GP address registrations.

Homes from the three groups were linked to individual residence records across the study period within WDS, providing start and end dates of residence.

The WIMD 2011 was used to obtain income-related deprivation data at the LSOA level. The urban/rural classification was obtained using the Office for National Statistics (ONS) classification. Person-level demographic data, including age and sex, were obtained from the WDS data set. When relevant, the date of death was obtained by linking the ONS death registration data to the WDS data set. When a conflict existed, the ONS deaths data set was used as the primary data source.

Data sets were set up in a panel design containing one record for each person within a home for each monthly period in which they were present in the study. Study entry dates were defined as the earliest date selected for either the date of moving into the property or the start of the study period (January 2005). Study exit dates were defined as the latest date selected for the month of death, date of moving out of the home or the end of the study period (December 2014). Variables such as comorbidity, outcomes and age were updated to be reflective of the specific period within the study.

Variables

Records of emergency hospital admissions for relevant conditions from 2005 to 2014 were extracted from the PEDW data set, which contains records of all inpatient and day case episodes of care undertaken in NHS Wales plus data on Welsh residents treated in other UK nations (primarily England). NWIS provides SAIL with a de-identified version of PEDW via monthly electronic feeds.

We selected the first episode from each case of emergency admissions, representing continuous periods of inpatient care for a single patient, for diseases indicated by the selection of specific International Classification of Diseases, Tenth Edition (ICD-10)85 codes. Total admissions were counted for each month a person was included in the study. Our primary outcome was defined as any admission for cardiovascular (codes I00–I99) or respiratory (codes J00–J99) reasons. Episodes representing symptoms and signs involving circulatory and respiratory systems (R00–R09) in the first diagnostic position with no subsequent secondary diagnosis codes were also included in the primary outcome.

The secondary cardiovascular outcome consisted of records with ICD-10 codes I00 to I99, with the respiratory outcome identified by ICD-10 codes J00 to J99. Admissions that were attributable to COPD were selected using a combination of age and ICD-10 codes: any age for admissions with codes J40–J44, or R06 primary diagnostic position combined with J40–J49 any position, and codes J45–J46 for those aged ≥ 40 years (see Appendix 7).

Comorbidity was calculated using Bottle and Aylin’s86 algorithm, which was created using English National Health Service Hospital Episode Statistics data. We amended the algorithm, opting not to include ICD-10 code C44 (Non-Melanoma Skin Cancer) within the comorbidity algorithm to avoid potential bias as a result of differential treatment practices, which can be carried out in primary or secondary settings depending on geographical location in Wales.

Bias

We were supplied with address details for 5801 homes, from which we were able to geocode 4968 (86%). The 14% loss of property data was a result of a number of reasons, including incomplete or poor-quality address data, properties not present within WDS or properties with no residents registered within the study period. This loss of properties represents potential selection bias; however, as a result of the anonymised nature of SAIL and information governance, we were unable to explore this in more detail. The largest risk of selection bias arises from the exclusion of 509 properties that we were unable to link in the WDS. An analysis of non-matched properties showed that 70% were multiple-occupancy residences (blocks and flats), with the remaining 30% predominantly in terraced housing. From our experience, these linkage rates are typical of secondary address-level administration data. 87 This indicates a potential issue with source data and classification of properties at the National Land and Property Gazetteer.

Loss to follow-up bias is avoided because of the use of routinely collected data in SAIL. We were able to follow participants over a long period retrospectively, allocating health-care utilisation to individuals for the full period they were resident within an intervention home. Potential bias arising from background trends in emergency hospital admissions was explored by comparing changes in rates of emergency hospital admissions between study groups over a long period, taking into account pre-, mid- and post-intervention health-care utilisation. The trends were comparable and required no specific adjustment.

Study size

The process described in Participants generated our study data set, comprising 25,908 people living within the 4968 intervention homes over the 10-year study period, allowing for people moving in and out of homes. We had comparable data on two comparator groups. The first, a social housing comparator group, contained 48,261 people living within 12,350 homes; the second, drawn from the top 10% of deprived LSOAs in Wales, contained 524,596 people living in 118,982 homes.

Quantitative variables

Two date fields were received in relation to the intervention: start and end date. The quality and extent of these data were varied; some properties had both start and end dates recorded, whereas other properties had either start or end dates or no dates at all. We reviewed the data and imputed intervention dates based on the logic described in this section. We assumed that the month of the intervention end date represented the start of the ‘after’ period, all data prior to this month being allocated to the ‘before’ data collection period. Although we completed a validation exercise to ensure that we were using the correct addresses of intervention properties, there was no available method to validate dates or intervention measure data. We applied rules to allocate property dates by following these steps:

1. reversed dates when end date was prior to start date (n = 22)

2. calculated median days between start and end date for all homes with valid start and end dates (median = 92)

3. for homes with a valid end date only, subtracted the median days to impute a start date

4. for homes with a valid start date only, added the median days to impute an end date

5. calculated median start and end dates for all homes after applying steps 1–4

6. applied the static start and end dates from step 5 across all remaining homes.

Statistical methods

The methodological approach, adopted for the primary and secondary outcomes and the subgroup analyses, is based on initial investigations to assess the nature of any trends present in the observed data over the study period. This observed data is available on a monthly basis and, for both primary and secondary outcomes, comprises counts of events in that month. In the absence of any obvious trend over time, data on each individual’s residence is conflated into two values, comprising the number of events occurring before and after the intervention. To take account of the different time durations in the pre- and post-intervention phases, these aggregated counts were transformed into annualised rates. These annualised rates were summarised and compared using mixed multilevel linear models featuring an indicator variable for phase, adjusting for explanatory factors and covariates, and incorporating random effects to account for clustering.

This approach takes the basic unit for clustering purposes to be a person’s unbroken period of residence in a property, so data on an individual arising from a second residence is regarded as independent of data collected during that individual’s first residence. This applies even if the two residences are the same, that is, when there is a break in a person’s residence at a property. The pre- and post-intervention phases are defined using the assumption that the intervention is effective from its end date. We set the phase indicator to be 0 for pre intervention and 1 for post intervention, so that the coefficient for this variable corresponds to the effect of the intervention.

We included several individual-level covariates and factors in our analyses. Specifically, we considered covariates summarising participant age for each phase, calculated using the mid-point of residence in an intervention study home; a seasonality score for each phase; a single comorbidity score, ranging from 0 to 1, summarising comorbidities recorded across all months; and an indicator of sex (male, female).

We also considered area-based variables recording income deprivation (summarised by five ordered categories ranging from 1 = least deprived to 5 = most deprived) and a measure of rurality (1 = village and hamlet, 2 = town and fringe, 3 = urban), both obtained at LSOA level. 88

We defined sine-based factors for each month, taking negative values for October to March inclusive and positive values for April to September inclusive, resulting in an aggregate factor of zero for each complete year. Our seasonality covariate was based on seasonality scores for each phase, defined as the sum of monthly factors across each phase.

To assess excess winter admissions, we created a binary indicator for winter or non-winter, set to 1 for December, January, February and March, and to 0 for all other months. 89

Our modelling approach, aimed at obtaining the precise estimate of the intervention effect on each variable in turn, used appropriate univariate linear mixed models (implicitly assuming normality) and progressed by eliminating, in turn and starting with the least significant, all covariates and factors with a coefficient with a p-value of > 0.05, concluding when all remaining explanatory variables were statistically significant.

Participants

Address records and intervention details for 5801 intervention homes were collated and supplied to SAIL for the intervention. There were 172 records with insufficient address data to allow data linkage. A further 99 records were excluded as a result of multiple source records matching to individual homes held within SAIL. A further 509 records were removed because there was no record of the home within the WDS data set. Finally, 53 records were removed when there were no residents recorded by the WDS as living in the home over the study period. This left 4968 properties for analyses, as shown in Figure 2. The supplied intervention addresses were validated against a separately sourced list of addresses from the Welsh Government, with 88% of addresses common to both sources. This is a conservative estimate because a number of addresses from both sources had insufficient address details to generate a linkable address. The number of individuals linked to these properties in the study period was 25,908.

FIGURE 2.

The flow diagram for the intervention group.

Descriptive data

Our final study size was 25,908 people living within 4968 intervention homes over the study period. We arrived at the study size through the process described in Methods, Participants and Results, Participants.

Properties

Just over 70% of intervention homes received one energy efficiency measure, around 20% received two measures and the remainder received three or more. The most common type of intervention measure carried out on the intervention homes was the installation of external wall insulation. Over 50% of homes received external wall insulation, 30% received photovoltaics, 20% received solar hot water, 15% switched fuels and 5% received an air source heat pump.

Individuals

We summarised the data by property and participant, because the interventions apply to properties but outcomes relate to residents. Each property can house multiple residents, who can be present simultaneously or consecutively, and each study participant can reside in multiple properties continuously or with breaks over the study period. We have demographic data for individuals living within 136,300 distinct study homes, of which 4968 are intervention homes, 12,350 are social housing comparator homes and 118,982 are comparator homes in areas designated in the top 10% of deprived areas by WIMD 2011.

There were 4968 properties that received the intervention (Table 1): for 2021 properties (40.7%), both the start and end dates for the intervention were known and for a further 1739 properties (35.0%), either the start or end date was known and the other was imputed. For the remaining 1208 properties (24.3%), both the start and end dates were imputed. Many people moved home during the intervention period. The extent of residential mobility is indicated by the association of several residents with multiple homes (Table 2).

Main results

Monthly emergency admission rates per person across the study period offer a visual confirmation of little or no trend in this rate (Figure 3). There were approximately three or four admissions per month per 1000 people throughout the study. Corresponding time plots for the comparator groups showed only weak correlation with the intervention cohort for the primary outcome, and considerable noise (see Appendix 8). Therefore, we did not use the comparator groups to control the analyses.

FIGURE 3.

Monthly emergency admission rates per person (study month 1 is January 2005) for residents within intervention homes.

Data and model summaries for our primary outcome and several secondary outcomes are presented, firstly for all ages (Table 3 and Figure 4) and then for older residents who are aged ≥ 60 years (Table 4 and Figure 5). All outcomes possess both more skewness and kurtosis than is consistent with the assumption of normality.

FIGURE 4.

Graphical representation of the intervention effects in Table 3 (with 95% CI) by emergency admission category for people of all ages.

FIGURE 5.

Graphical representation of the intervention effects in Table 4 (with 95% CI) by emergency admission category for people aged ≥ 60 years.

The intervention did not have a statistically significant effect on our primary outcome, neither did it have a significant effect on any of our all-age secondary outcomes. Table 3 and Figure 4 show that the intervention was not significantly associated with a change in cardiorespiratory, COPD-related, cardiovascular or respiratory emergency admissions for people of all ages. The results include summaries of the raw, unadjusted data for the pre- and post-intervention phases, and the paired differences for those people who were in the study for both phases (irrespective of the lengths of residency periods). We subsequently included covariates and factors in univariate linear models for each outcome, and the adjusted comparisons are taken from models that retain all significant covariates and factors (listed at the end of Tables 3 and 4). Age was a significant covariate in all ‘all ages’ models.

Estimates of overall intervention effects are small – for instance, the estimated Δ = 0.0011 for the primary outcome equates to 1.1 further cardiorespiratory emergency admissions per year per 1000 people – and generally consistent with the differences in pre- and post-intervention rates. However, widths of the 95% confidence intervals (CIs) for the intervention effect vary quite considerably across outcomes, reflecting both prevalence and variability of that outcome in study data. There is only moderate agreement between the (adjusted) intervention effects and the (unadjusted) paired differences in rates for those in the study for both phases. More detailed consideration of the characteristics of that subgroup may further reconcile these summaries.

Figure 5 shows the associations of the intervention with changes in cardiorespiratory, COPD-related, cardiovascular or respiratory emergency admissions for people aged ≥ 60 years. This is a relatively small subgroup, so interpretation of these results should take account of the reduced sample size. The intervention was not linked to significant changes in emergency admissions for cardiorespiratory, COPD-related and respiratory conditions. However, it had a significant effect on cardiovascular-related emergency admissions. In contrast to expectations, there was an increase in admissions in the post-intervention period.

In order to determine the excess winter hospital admissions for the primary outcome of the study (the annualised rate of combined cardiovascular or respiratory emergency admissions per person), we classified months as winter (December to March) or non-winter (April to November). Table 5 summarises the observed rates by phase (pre or post intervention) and season (winter or not winter).

Table 5 shows that, as per intuition, rates are higher in the winter months than in the non-winter months in both the pre- and post-intervention phases. In this analysis, we are also interested in the interaction between intervention phase and season. This is because the statistical interaction summarises the extent to which differences in admissions occur between seasons for each of the pre- and post-intervention phases separately. Table 5 therefore presents details from the interaction analysis for this term (Δ_PS), adjusted for comorbidity score and sex (both with p < 0.001). The interaction between season and intervention phase was not significant.

Key results

The study found no intervention effect of reduced admissions for either the primary outcome (combined cardiovascular and respiratory emergency admissions) or any of the secondary outcomes for people of all ages living in an intervention home. It also did not find an intervention effect of reduced cardiorespiratory emergency admissions when we focused analyses on residents who were aged ≥ 60 years. However, we did see a statistically significant intervention effect of increased cardiovascular-related emergency admissions for residents aged ≥ 60 years. Cardiorespiratory emergency admission rates were found to be higher in winter than in non-winter months, in both the pre- and the post-intervention phases. The interaction between season and phase was not statistically significant, so there was no evidence that the intervention had an effect on the difference between winter and non-winter rates.

Limitations

Routine data allowed us to evaluate this intervention using retrospective links from individuals living in intervention homes for the relevant times. We were able to retrospectively analyse health-care utilisation data for a large number of people across a 10-year period and minimise the bias experienced in more-traditional research caused by factors such as recruitment and subsequent loss to follow-up. Problems of recall bias are avoided with routinely collected health data that are based on observed health events and not subjectively reported conditions.

However, we were unable to randomise participants into intervention and control groups and, as with all observational studies, the potential for unmeasured confounding remains. For example, it is challenging to control for the multiple associations between poverty, poor housing and poor health. 90

The study was only able to determine the impact of the intervention on events recorded as hospital admissions. The lack of association with emergency hospital admissions indicated that benefits do not appear in the hospital statistics within the follow-up period and that future evaluations should focus on less-severe conditions that may be treated in primary care settings, although recent research suggests that housing interventions may not necessarily change established patterns in primary health-care utilisation in populations with a long-term lack of well-being. 91

Furthermore, we acknowledge the data limitations, including the lack of depth of the routine data. For instance, using routine data means that we cannot understand how people’s lives have changed in their home; this needed the additional studies that were completed as part of this research (see Chapter 3). Data quality was also an issue. Intervention home addresses and intervention dates required considerable time and effort to collect, and subsequently convert to a structured format that could be used within the databank. There were missing dates for several hundred intervention homes.

We relied on a routinely collected demographic data set (WDS) to link people into homes for the correct time periods. Research by the ONS suggested that some segments of the younger male population are more likely to be missing from this data set. Further work is needed to quantify potential bias in this routine anonymised data set.

Finally, we acknowledge that assumptions implicit in linear models are unlikely to be entirely satisfied by the study data, and that it would be useful to investigate further models that seek to account more explicitly for features observed in this data.

Interpretation

There was no evidence that energy efficiency investments, as implemented in the intervention programme, provided a reduction in health-care utilisation in the short to medium term. Residents were not involved in the intervention implementation and so may have felt a lack of control; this may have contributed to the lack of a significant reduction in health-care events. 92 Longer-term studies, of a decade or longer, may be needed to realise an intervention effect on health-care utilisation recorded using routine data, including hospital as well as primary care outcomes.

Generalisability

The research is generalisable to residents of homes located in temperate regions, with similar socioeconomic characteristics, living in homes in need of thermal efficiency measures. The intervention homes were predominantly social housing, maintained by LAs and RSLs and located within low-income areas. The results may also be generalisable to some extent to residents of private rented homes or homeowners in low-income areas.

Study design

The community-based study used a quasi-experimental controlled pre-/post-test design and collected data through self-completion questionnaires. Questionnaires were distributed in low-income areas where energy efficiency improvements were scheduled but had not yet started, as well as in matched control areas where no energy efficiency improvements were scheduled. The intervention programme ran for 3 years between 2012 and 2015. The community-based study focused on schemes that were delivered in 2014 and 2015, respectively.

Setting

The energy efficiency investment programme targeted low-income mixed-tenure neighbourhoods. The schemes were selected on the basis of the number of low-income households, the number of households owning or privately renting their house and the number of hard-to-heat, hard-to-treat homes in the area. The schemes mostly took place in Strategic Regeneration Areas with high numbers of hard-to-heat, hard-to-treat homes. Matched control areas were selected using the WIMD and with the assistance of the LAs where the schemes were taking place. In total, 24 intervention and 23 control areas were included in the study. Anglesey was the only scheme that did not have a direct matched control area. Figure 6 shows the locations of the intervention areas that were included in the study.

FIGURE 6.

Locations of the intervention areas.

Baseline (pre-intervention) data for year 2 schemes were collected during the 2013/14 heating season, before energy improvement work had started on homes scheduled to receive the intervention. Follow-up (post-intervention) data for year 2 schemes were collected during the 2014/15 heating season, after the work was completed. Baseline and follow-up data for year 3 schemes were collected during the 2014/15 and 2015/16 heating seasons, respectively. Data for the intervention and control areas were collected during the same time periods. Data for one year 2 scheme (Gwynedd) could not be collected in two subsequent heating seasons as a result of delays in the delivery of the improvements. In this case, the follow-up data for both the intervention and matched control area were collected during the 2015/16 heating season, at the same time as the follow-up data for year 3 schemes.

Participants

We used a purposive sampling strategy to recruit residents living in the eligible intervention and control areas. The survey was administered using the drop-off-and-collect method of data collection. 93 Initial contact was made by postal letter, introducing the study and informing residents that they were going to be visited by researchers from the university. Researchers then visited all selected areas to deliver the questionnaires by hand and, when possible, personally invite residents to take part in the study. When at the time of delivery no residents were at home, a pack containing a cover letter, questionnaire and Freepost envelope was left in their letter box. Researchers then returned at a later date, usually within a week, to collect the questionnaires. Similarly, a reminder to return the questionnaire was left if occupants were away at the time of the return visit. The questionnaire could then be returned by Freepost. Participants were asked to provide their contact details and consent to be recontacted for the follow-up phase of the study. Any adult resident currently living in the selected intervention and control areas was eligible for inclusion.

The initial invitation letter and the questionnaire were both translated into Welsh. The Welsh version of the questionnaire was available on request.

All participants who had returned a completed questionnaire in the baseline period and had consented to be recontacted were invited to fill out a second questionnaire for the follow-up. Participants were sent a postal questionnaire that was addressed to them personally. They were subsequently visited by researchers to collect the questionnaire in person when possible. A reminder was left if the participants were not at home during the follow-up visit.

Incentives were used to increase the baseline and follow-up response rates. Participants were entered into a prize draw for one of 25 £50 shopping vouchers (year 2 baseline) or for one of three iPads (Apple Inc., Cupertino, CA, USA) (year 3 baseline and all follow-up stages).

Not every eligible household within the scheme areas elected to have energy efficiency work done to their house. Records from the two scheme managers were used to confirm which properties were upgraded and which improvements were made. Respondents from intervention areas who did not have energy efficiency work done to their home became part of the control group. A small number of properties located within the matched control area of a delayed year 2 scheme (Gwynedd) became part of a year 3 scheme. Respondents from these properties became part of the intervention group.

Variables

Data were collected via a self-completion questionnaire covering the topics of health and well-being, fuel poverty, financial difficulties and stress, food security, social interactions, thermal satisfaction, housing conditions and number of heated rooms. The sociodemographic section of the questionnaire contained questions about sex, age, household composition, marital status, employment status, household income, smoking and housing benefits (see Appendix 9).

The primary health outcomes were changes in mental health status [MCS from the Short Form questionnaire-12 items (SF-12)] and self-reported respiratory and asthma symptoms. Secondary health outcomes were changes in self-reported health-related quality of life [Physical Health Composite Scale (PCS) from the SF-12] and subjective well-being. Other secondary psychosocial outcomes included changes in fuel poverty status, financial difficulties and stress, food security, social interactions, thermal satisfaction and reported housing conditions.

Bias

The community-based study reported in this chapter used a quasi-experimental, controlled pre-/post-test design to control for time-variable factors such as external hydrothermal conditions and other temporal trends. The assignments of participants to the intervention and control groups was not randomised. Selection bias occurs when selection to the intervention and control groups results in differences in unit characteristics between conditions that may be related to outcome differences. 106 In order to maximise initial comparability, the matched control areas were selected using the same criteria as the intervention schemes.

The drop-off-and-collect method of survey administration and incentives were used to reduce selection bias as a result of non-response as much as possible. 93 The overall response rate was 16.5%, with 1508 of the 9127 distributed questionnaires being completed and returned. Of the 1508 baseline respondents, 1288 consented to be recontacted (85.4%). The attrition rate between baseline and follow-up was 48.1% owing to a lack of consent and loss to follow-up (n = 726), resulting in a final total sample of 782 respondents who filled out both the baseline and follow-up questionnaires (Figure 7).

FIGURE 7.

The flow diagram for the community-based study.

The overall response for the baseline data collection rates were similar for the intervention and control groups (15.0% vs. 17.9%), although there were some differences in attrition (44.5% vs. 50.9%) between the baseline and follow-up phases [χ²(1) = 6.132; p = 0.013]. Differences were also seen in the rate of consent between the intervention and control areas (89.0% vs. 82.6%) [χ²(1) = 12.165; p = 0.000]. The resulting intervention and control populations were comparable in terms of sociodemographics, with chi-squared tests showing non-significant differences between the two groups for all variables listed.

A loss to follow-up analysis showed that there were a number of socioeconomic differences between the respondents included in the final study sample and those who dropped out between baseline and follow-up (Table 6). Respondents lost to follow-up were more likely to be female [χ²(1) = 9.661; p = 0.002], younger in age [χ²(7) = 73.053; p = 0.000] and have children living in the household [χ²(1) = 28.738; p = 0.000]. Respondents lost to follow-up were also more likely to have a lower household income [χ²(8) = 15.950; p = 0.043] and to receive housing benefits [χ²(1) = 8.763; p = 0.003]. In terms of health outcomes, the respondents lost to follow-up were more likely to be at risk of common mental disorders, as measured by the MCS of the SF-12 [χ²(1) = 8.594; p = 0.003]. However, there were no differences with regard to physical health, as measured by the PCS of the SF-12, subjective well-being and self-reported respiratory and asthma symptoms.

Recall bias may be another possible source of bias, which was minimised by asking respondents to answer questions regarding the current heating season. Missing data bias is possible when respondents may have chosen not to answer specific questions in either questionnaire. Overall, there were few missing values, except for self-reported asthma symptoms. A missing-values analysis found that data were missing completely at random.

Study size

We aimed to achieve a total sample size of 1000 participants (intervention, n = 500; control group, n = 500) to have 80% statistical power to detect an effect size (d) of 0.16 at the 5% significance level. The final achieved samples of n = 364 for the intervention group and n = 418 for the control group provide 80% statistical power to detect effect sizes of d = n = 0.18 at the 5% significance level, which is in line with effect sizes observed in comparable field studies examining the short-term health effects of housing improvements. 48,51,107

Statistical methods

Statistical analyses were conducted with IBM SPSS Statistics version 20.0 (IBM Corporation, Armonk, NY, USA) and MLwiN version 2.36 (MLwiN, Centre for Multilevel Modelling, Bristol, UK) software packages. 108–110 The effects of the intervention on the primary and secondary health and psychosocial outcomes were initially assessed using mixed design analyses of variance (ANOVAs) as proposed, and subsequently using a multilevel modelling, repeated measures approach. The two types of analyses produced similar results. Here we only present the results of the multilevel modelling analyses for the purpose of clarity.

A longitudinal data set was created with the two measurement occasions (level 1) nested within individuals (level 2), allowing the analyses to take into account non-independence between measurement occasions. The basic model included the intervention group (intervention vs. control) as an individual-level factor and measurement occasion (follow-up vs. baseline) as a within-person factor. Differential changes between the intervention and control groups were assessed with a cross-level interaction between measurement occasion and intervention group. Only the interaction effects indicating the differential changes between the intervention and control groups are reported. All analyses were conducted with and without adjusting for the covariates selected a priori: sex, age, housing benefit, household income and smoking status. Cohen’s d was calculated to determine the size of interaction effects. Cohen’s d is a standardised measure of the magnitude of an effect, with the values of 0.2, 0.5 and 0.8 generally taken to reflect ‘small’, ‘medium’ and ‘large’ effect sizes, respectively. 111,112

Different types of models were constructed depending on the type of outcome variable. Linear regression models were constructed for the primary health outcomes of respiratory symptoms, asthma symptoms, MCS, the secondary health outcomes of PCS and subjective well-being, as well as for the secondary psychosocial outcomes of financial difficulties and food security. Ordered multinomial response models were constructed for the ordinal psychosocial outcome variables of financial stress, thermal satisfaction, satisfaction with the current state of repair of their home, number of reported housing problems and the number of heated rooms during the day and the evening. Logistic regression models were constructed for the two secondary psychosocial outcomes of fuel poverty and social interactions. For the ordered multinomial response and binomial models, a logit link function was used. Parameters in all models were estimated using Markov chain Monte Carlo with 50,000 iterations. All analyses were conducted with and without adjusting for the individual-level covariates of sex, age, housing benefits, household income and smoking status. The five covariates were selected a priori.

For the SF-12, missing data were dealt with using QualityMetric’s Missing Score Estimation algorithm (QualityMetric, Lincoln, RI, USA), for which item response theory and regression methods were used to estimate scores on the health domain scales and component summary measures (MCS and PCS) using QualityMetric’s Health Outcomes Scoring Software (QualityMetric, Lincoln, RI, USA). 113 All other missing data were excluded from the statistical analyses, which were conducted without imputation, as the percentage of missing values were in most cases low (< 3%). The missing values were higher for asthma symptoms (8.8%). Little’s MCAR (missing completely at random) tests found that the data were missing completely at random [primary and secondary health outcomes and sociodemographic characteristics: χ²(26) = 28.745; p = 0.323; psychosocial outcomes: χ²(60) = 63.720; p = 0.347].

For the analysis of health-related quality of life and QALYs, the SF-6D index values were transformed into utilities implementing the area under the curve approach, with these values baseline-adjusted. A linear progression of SF-6D between baseline and follow-up was assumed in the absence of more data. For the main analysis, a multilevel modelling, repeated measures approach was used, adjusting for the individual-level covariates of sex, age, housing benefits, household income and smoking status.

Participants

In total, 9137 questionnaires were distributed to eligible households across 47 intervention and control areas at the start of year 2 and year 3 of the intervention programme (see Figure 6). Of these, 1508 were completed and returned (656 from the intervention and 852 from the control areas), corresponding to an overall response rate of 16.5%. Figure 7 illustrates the flow of participants through the study.

Out of the 1508 baseline participants in both the intervention and control groups, 220 did not consent to be recontacted and a further 506 participants were lost to follow-up, reflecting an overall attrition rate of 48.1%. Eighty-one participants from the original intervention areas did not receive any upgrades to their home as part of the intervention programme. These respondents were added to the control group. Some of the properties in the matched control area for the delayed year 2 scheme in Gwynedd were included in a year 3 scheme before follow-up data could be collected. The 22 respondents from these properties were added to the intervention group.

Descriptive data

Table 7 summarises the final study sample in terms of sociodemographic and building characteristics. The intervention and control populations were comparable in terms of sociodemographic and building characteristics, with chi-squared tests showing no significant differences between the two groups for any of the variables listed in the table. Because the intervention and control group are largely similar at baseline, there is a low likelihood of confounding.

Of the 782 respondents who completed both the baseline and follow-up questionnaires, the highest proportion was female, aged ≥ 65 years, did not live with children within their household, was either married or cohabiting and was retired. The highest proportion of respondents had no formal educational qualification, had a combined household income of £10,000–19,999. One-quarter of all respondents received housing benefits, reflecting the overall levels of deprivation of the intervention and control areas. The vast majority of respondents owned the properties they resided in and had lived in the same property for > 9 years. The building type tended to be either semi-detached or terraced, built either before 1919 or before 1945, with an average of three bedrooms.

External wall insulation was by far the most implemented measure (71.7%), followed by voltage optimisers (44.4%) and full central heating systems (new condensing boilers and radiators and pipes when needed; 39.0%). Respondents from three communities received a connection to the mains gas network together with a new heating system (13.9%). Voltage optimisers were only implemented in South Wales schemes.

Main results

Key results

This was the first large quasi-experimental field study with a controlled pre-/post-test design to examine both the short-term health and psychosocial impacts of energy efficiency investments in low-income areas. This community-based study found no evidence that investments in energy efficiency improve respiratory or mental health in the short-term. Furthermore, no evidence was found that they provide physical health benefits in the short-term. However, those who received energy efficiency measures reported improved subjective well-being as compared with the controls, as well as improvements in a number of the secondary psychosocial outcomes that are conducive to better health. The study found that respondents who received the intervention also reported fewer financial difficulties, higher thermal satisfaction and higher satisfaction with the improvement of their homes. They also reported less reluctance to invite friends or family to their homes. The results were similar with or without controlling for a number of socioeconomic covariates.

Limitations

The field study in this chapter used self-completion questionnaires to be filled out by the study participants themselves. It is therefore subject to a number of biases. The study had a low initial response rate and a substantial loss to follow-up. However, the response and attrition patterns were similar for the intervention and control areas, and an analysis showed that there were only a small number of differences between study respondents and those lost to follow-up. The final samples appeared largely comparable in terms of their composition. The low response and retention rates are perhaps not completely surprising given the nature of the research. The study was conducted in low-income neighbourhoods, where response rates for mail and door-to-door data collection methods tend to be low. 114 Several strategies were used to increase the response rates, including incentives and door knocking.

In order to make the control group as comparable as possible to the intervention group, the matched control areas were selected using the same criteria as the intervention areas. This proved to be challenging, given that many comparable areas had already received energy efficiency measures through the intervention programme. A number of control areas were subsequently selected to receive energy efficiency investments in the year after the study. The composition of the final samples suggest that the control participants may be used as a robust ‘non-exposed’ comparator group.

A further limitation is the time frame of the study. Outcome measures were collected in the heating seasons directly before and after the intervention. The short follow-up period means that claims can only be made about the short-term effects of the intervention (see Interpretation). Studies with longer follow-up periods are needed to establish the long-term impacts of energy efficiency investments. 48 This has been done in the data linkage study (see Chapter 2).

According to Thomson et al. 48,115 interventions targeting at-risk populations provide clearer health benefits than area-based housing improvement programmes. The benefits of area-based programmes may be less pronounced because they do not target those who are most at need. Unlike other demand-led schemes such as Warm Homes Nest, the Warm Homes Arbed intervention was not tailored according to individual need. However, the intervention did target low-income areas with inadequate warmth owing to a large number of hard-to-heat, hard-to-treat homes within the area. Still, no clear physical health improvements were observed in this study, which may be explained by the limited follow-up period in the research. It would be useful to directly compare area-based (e.g. Warm Homes Arbed) and demand-led, targeted (e.g. Warm Homes Nest) schemes.

Researchers evaluating complex social interventions are faced with several challenges. 116,117 The study involved an evaluation of an external, in this case government-led, programme. That means that the researchers did not have control over the content or delivery of the programme. Furthermore, the intervention effects may be diluted by constant changes in the context. For example, it is possible that respondents may have independently chosen to undertake energy efficiency improvements to their home, therefore diluting the effects of the intervention programme. 117,118 However, there is no evidence that this happened in the study.

Interpretation

The study suggests that, although there is no evidence that energy efficiency investments provide physical health benefits in the short term, they improve social and economic conditions that are conducive to better health. Furthermore, they were found to be beneficial for subjective well-being. Longer-term studies are needed to establish the health impacts of energy efficiency investments. According to Thomson et al. ,48,115 most studies investigating the health impacts of housing improvements have limited follow-up periods. Studies have therefore been unable to detect longer-term health impacts. We would expect that the changes in the psychosocial outcomes are conducive to better health in the longer term. The observed changes in the social outcomes may be a valuable indicator of the potential for longer-term health benefits.

Generalisability

The results are likely to be generalisable to other low-income areas with inadequate warmth and other vulnerable at-risk populations. The public health implications are typical for other deprived areas across the UK with low-quality housing. The results may be less generalisable to other less-deprived areas.

Study design

The household monitoring study uses a quasi-experimental controlled before-and-after design consisting of long-term hydrothermal condition monitoring in two subsequent heating seasons. The monitoring took place in a number of households before and after they received energy efficiency improvements under the intervention programme. The study further included a number of control households that did not receive such improvements. The indoor measurements for the control households were taken at the same time as for the intervention households. All households for the monitoring study were recruited from the community sample described in Chapter 3.

Setting

The study was conducted in five low-income areas where energy performance investments were scheduled and in five matched control areas where no such investments were planned (Figure 8). The baseline measurements were taken in the 2013/14 heating season. The follow-up measurements were taken in the 2014/15 heating season.

FIGURE 8.

Locations of the intervention and control areas.

The five intervention and control areas were selected from year 2 schemes included in the community-based study (see Chapter 3). The intervention areas and their matched control areas were in Brynamman (Carmarthenshire), Caerau (Cardiff), Llay (Wrexham), Hollybush (Caerphilly) and Pennydarren (Merthyr Tydfil). The areas were selected based on the scheduling of the intervention work and the returns of the baseline questionnaires from the community-based study. This was to ensure that a sufficient number of households could be recruited in time for the monitoring to take place in the 2013/14 heating season. The communities varied in terms of their location, climatic conditions and dominant housing type. The Cardiff and Merthyr Tydfil areas consisted predominantly of British steel-framed [British Iron and Steel Federation (BISF)] houses, Caerphilly and Carmarthenshire were off-gas areas and Wrexham consisted predominantly of terraced houses with solid walls. The control areas were selected to resemble the intervention areas as much as possible in terms of housing type and level of deprivation (see Chapter 3).

Respondents from the selected areas who provided consent to be recontacted were invited by telephone to have their house monitored. In total, 99 households agreed to take part in the study, of which 50 were located in the intervention areas and 49 in the matched control areas. Households were visited between 11 January and 1 February 2014 to install indoor data loggers, and again between 25 March and 17 April 2014 to collect them. In the baseline period, houses were monitored for a minimum of 28 consecutive days and a maximum of 71 days. On average, the houses were monitored for 46 days, with a SD of 9 days.

The households that took part in the first part of the study were recontacted by letter prior to the 2014/15 heating season for follow-up measurements. The reminder letter was followed up by a telephone call to arrange an installation visit. Households were visited between 1 November and 18 November 2014 to install indoor data loggers, and again between 12 April and 30 April 2015 to collect them. In the follow-up period, houses were monitored for a minimum of 97 days and a maximum 181 days. On average, houses were monitored for 127 days (SD 32 days). Loss to follow-up was low (11%), resulting in a final sample of 88 households (intervention, n = 48; control, n = 40). Local weather stations were installed in or close to the five monitoring areas to record external meteorological conditions during the baseline and follow-up periods. Gas and electricity meter readings were taken during the installation and collection visits.

Participants

Households for the monitoring study were recruited from the community sample described in Chapter 3. The aim was to recruit 100 households for the monitoring study, with a subset of households undergoing energy efficiency improvements (n = 50) and a control group that did not receive such improvements (n = 50).

Variables

The following exposure intervention and outcome variables were included in the analyses.

Intervention measures

The intervention measures included external wall insulation (with mechanical ventilation), new windows and doors, boiler and heating system upgrades, connection to the gas mains network and installation of voltage optimisers. The measures were recorded for each participating household. In this study, 35 households received external wall insulation, nine received new windows and doors, 48 received a new boiler or heating system and 46 had a voltage optimiser installed. Furthermore, 20 properties from two intervention areas were connected to the mains gas network. Figure 9 shows that, on average, the measures increased the Standard Assessment Procedure ratings of the intervention households from 52 (SD 12) to 66 (SD 5). This is an average increase from Energy Performance Certificate rating band E to band D. The Standard Assessment Procedure was developed by the Building Research Establishment and is currently the methodology used by the UK Government to assess the energy performance of dwellings. 123 It presents the energy performance of homes in a figure ranging from 1 to 100. This has been subdivided into seven bands ranging from A to G.

FIGURE 9.

Standard Assessment Procedure ratings of intervention households before and after installation of the energy efficiency measures.

Bias

The household monitoring study was undertaken in a subset of households that had already participated in the community-based study. The biases described in Chapter 3 therefore also apply to this part of the project.

Another potential bias was that the local climate could lead households in different areas to be exposed to different external hydrothermal conditions during the baseline and follow-up. To control for such biases, the study compared internal conditions of the intervention households with the control households located within the same areas. Furthermore, internal hydrothermal conditions were adjusted for external hydrothermal conditions as measured by weather stations installed in or near the different monitoring areas. This design minimised differences between households resulting from external hydrothermal conditions.

Selection and attrition bias have the potential to overestimate and underestimate the effects of the intervention. The household monitoring was undertaken in a subset of households that had already participated in the community-based study (see Chapter 3).

There was a risk of selection bias in the households agreeing to their house being monitored, as well as attrition bias between the baseline and follow-up monitoring. Households that had completed the questionnaire and consented to be recontacted were invited to participate in the monitoring study. The monitoring households and the overall sample from which they were selected were broadly similar in terms of their building and sociodemographic characteristics. The monitoring sample contained a higher percentage of terraced houses (47.9% vs. 29.0%) and private rentals (11.5% vs. 4.3%) than the overall area sample. Figure 10 shows that the response rate for the intervention group (23.3%) was slightly lower than that for the control group (30.2%). However, that was mainly owing to the size of the area sample from which they were recruited. Attrition was higher for the control households (n = 9) than for the intervention households (n = 2), but no monitored area lost more than four households. A loss to follow-up analysis showed that attrition did not bias the samples in a systematic way. The final intervention and control samples were comparable in terms of building age, building type, number of bedrooms, tenure and household composition (i.e. with or without children) (see Table 11).

FIGURE 10.

The flow diagram for the household monitoring study.

Study size

The study set out to monitor 100 properties over a 4-week period in two subsequent heating seasons. The 15-minute interval readings were combined to calculate whole-day averages, as well as averages for 4-day segments (i.e. morning, day, evening and night). This would ensure that the statistical analyses were based on ≥ 5600 data points clustered within the 100 households.

The eventual sample consisted of 99 households that were monitored for an average of 46 days (SD 9 days) during the baseline period and 88 households that were monitored for an average of 127 days (SD 32 days) for the follow-up period. This created a database with 15,771 data points for the different hydrothermal outcome variables after the removal of missing day values. All measurements were included in the final data set. This means that all 99 households contributed to the baseline estimates, but only the measurements of the 88 households included in both the baseline and follow-up contributed to the estimates for changes over time. This means that the parameters reported in this report were based only on the monitoring data of 88 households for which we had both baseline and follow-up periods.

Statistical methods

The data were analysed by constructing a series of controlled multilevel interrupted time series regression models, with daily internal conditions (level 1) nested within households (level 2) that either received an intervention or did not. The nested multilevel design makes it possible to take account of the clustering of the observations over time using random effects. 130 The approach also enables the handling of unbalanced data when the number of observations differ for the different households and time periods. 130 This makes the approach suitable for analysing monitoring data of multiple properties with different start and end dates.

Analyses were conducted with the MLwiN version 2.36 software package. 109 The software package is specifically designed for fitting multilevel models, in this case an interrupted time series regression analysis. The analysis involved the use of the time series of the daily averaged hydrothermal conditions that were measured during the baseline and follow-up periods in the intervention and control households. The interruption occurred between baseline and follow-up sampling periods when intervention households had improvement work done to their homes. Therefore, the interruption in the ‘interrupted time series’ refers to the energy efficiency improvements undertaken in the intervention households. This was then compared with control households that did not receive the energy efficiency investments during that period.

The basic statistical models included three independent variables: (1) the intervention group, (2) the measurement period and (3) an interaction between measurement period and intervention group. The intervention group variable indicated whether the measurements were taken in an intervention or a control household. The measurement period variable indicated whether the measurements were taken in the baseline or the follow-up period. The interaction term of the measurement period and intervention group variables indicated that the intervention has taken place in the follow-up period for the intervention households. The regression coefficient related to this term shows the level of change in internal conditions for the intervention group relative to the control group.

The statistical models were further controlled for external conditions. This was done by including the daily averaged external measurements as independent variables. The models with indoor air temperature as the outcome variable included daily HDD values as a covariate to control for external thermal conditions. The models with indoor RH as the outcome variable additionally included a measure of the average daily outdoor RH to control for external hydrological conditions.

Interrupted time series analyses typically include a time variable (indicating the time elapsed since the start of the study, as measured in days) and a time after the interruption variable (indicating the time elapsed since the intervention, as measured in days) in order to identify trends over time and changes in the trend after the intervention, respectively. 131 However, as no obvious trend over time was observed within the baseline and follow-up periods, these terms were excluded from the regression models.

One problem with repeated measurement data is that the measurements are often not independent, which violates one of the assumptions of ordinary least squares regression. Autocorrelation within time series, when measurements close to one another are more similar than measurements that are further apart, may lead to increased type 1 errors. The autocorrelation function and partial autocorrelation function in MLwiN indicated autocorrelation with a diminishing lag. Autocorrelation reflects the internal correlation within a time series, showing the degree to which the different measurements are interdependent. 131 An autoregressive model was constructed by adding a weight specifying that the error covariance decreases as the time distance between measurements increases in order to control for the observed dependency. 132

Participants

The household monitoring study took place in five intervention areas and their matched control areas nearby (see Figure 8). Respondents from these areas who provided consent to be recontacted were invited to have their home monitored. In total, 202 households were invited by telephone to participate, of which 99 agreed to have their house monitored (intervention, n = 50; control, n = 49). This corresponds to a response rate of 49%. The rest of the households were not contacted, either because they did not provide a contact telephone number or because the maximum number of households for the area was reached. Eleven households were lost to follow-up owing to ill health or relocation (intervention, n = 2; control, n = 9). This means that 99 households were monitored at baseline and 88 households at follow-up. Figure 10 shows the flow of households through the monitoring study.

Descriptive data

Table 11 summarises the characteristics of the intervention and control households at baseline and follow-up. It shows that there were no statistically significant differences between the two groups in terms of building age, building type, number of bedrooms, tenure and household composition.

Table 12 shows the average internal conditions for the intervention and control households at baseline and follow-up, unadjusted for external conditions. The table suggests that indoor air temperatures increased for the intervention group but decreased for the control group between baseline and follow-up. The changes in indoor RH were less pronounced. Small reductions were observed for both the intervention and the control groups. The internal conditions presented in the table are not adjusted for external hydrothermal conditions, which may differ across the monitoring periods and areas.

Table 13 shows the distribution of internal conditions for the intervention and control groups at baseline and follow-up, again unadjusted for external conditions. The figures represent the proportion of measurements falling into the different indoor air temperature and RH bands. The distribution of indoor air temperature was similar for the two groups at baseline [χ²(3) = 1.761; p = 0.623] but differed at follow-up [χ²(3) = 18.231; p = 0.000]. The proportion of substandard indoor air temperature measurements decreased for the intervention group but increased for the control group. In contrast, the proportion of indoor air temperature within the 18–24 °C band (the recommended comfort zone) increased for the intervention group but decreased for the control group.

Furthermore, Table 13 shows that the proportion of substandard RH measurements (i.e. > 60% RH) decreased for both the intervention and control groups. The distribution of indoor RH levels was similar at baseline [χ²(3) = 2.659; p = 0.447] and at follow-up [χ²(3) = 3.001; p = 0.391].

Main results

Indoor air temperature

Figure 11 shows the estimates and 95% CIs of the measurement occasion × intervention group interactions for the overall average whole-house temperature, and for the average whole-house temperatures in the morning, day, evening and night, respectively. These interactions indicate the levels of change in indoor air temperature observed in the intervention households in comparison to the control households. The figure shows that, on average, the intervention increased the indoor air temperature by 0.84 °C (95% CI 0.64 to 1.04 °C). The largest changes were observed in the evening (1.17 °C, 95% CI 0.94 to 1.39 °C) and at night (1.01 °C, 95% CI 0.79 to 1.24 °C). Slightly smaller changes were observed in the morning (0.51 °C, 95% CI 0.26 to 0.75 °C) and during the day (0.62 °C, 95% CI 0.40 to 0.85 °C).

FIGURE 11.

Relative change in daily average indoor air temperature during different times of the day for the intervention households.

Figure 12 shows that significant increases in indoor air temperatures were found for the living room and bedroom. On average, the intervention increased the indoor air temperature of the living room by 1.01 °C (95% CI 0.78 to 1.23 °C) in comparison to the control households. The largest change was observed in the bedroom: bedroom temperature in intervention households increased by an average of 1.28 °C in comparison to control households (95% CI 1.04 to 1.52 °C). The increases in the kitchen were the smallest and non-significant (0.24 °C, 95% CI –0.01 to 0.48 °C).

FIGURE 12.

Relative change in daily average indoor air temperature for different rooms of the intervention households.

Figure 13 shows that some intervention measures were more effective than others in raising indoor air temperatures. External wall insulation produced the largest increase in indoor air temperature (1.12 °C, 95% CI 0.69 to 1.55 °C). Connecting a property to the gas mains network also increased the indoor air temperature significantly by an average of 0.69 °C (95% CI 0.29 to 1.09 °C). A new boiler or heating system (–0.19 °C, 95% CI –0.69 to 0.31 °C) and new windows and doors (–0.02 °C, 95% CI –0.39 to 0.35 °C) did not increase indoor air temperatures significantly.

FIGURE 13.

Relative change in daily average indoor air temperature for different intervention measures.

The effects of the intervention on indoor air temperatures were different for the different building construction types. Figure 14 shows that the intervention increased indoor air temperatures in buildings with solid walls (1.54 °C, 95% CI 1.26 to 1.83 °C) and in British steel-framed (BISF) buildings (0.74 °C, 95% CI 0.51 to 0.96 °C). The intervention did not increase indoor air temperature in buildings with cavity walls (–0.17 °C, 95% CI –0.58 to 0.25 °C).

FIGURE 14.

Relative change in daily average indoor air temperature for different construction types.

Figure 15 shows the change in indoor air temperatures as a result of the intervention under different heating demand conditions. The increases in indoor air temperature ranged between 0.59 °C and 1.03 °C, and were the highest for the lower heating demand conditions (i.e. below 6 HDDs and between 6 and 8 HDDs).

FIGURE 15.

Relative change in daily average indoor air temperature under different heating demand conditions for the intervention households.

Indoor relative humidity

Figure 16 shows that, on average, the intervention increased indoor humidity levels by 0.04% RH in absolute terms. The increase in the intervention households was not significantly different from the one observed for the control households (95% CI –0.74% to 0.83% RH). The figure further shows that the changes were consistent for different levels of outdoor RH conditions. None of the changes differed significantly from the changes observed for the control households under the same conditions.

FIGURE 16.

Relative change in daily average indoor RH under different external RH conditions for the intervention households.

Figure 17 shows that the different intervention measures had differential impacts on internal hydrological conditions. Both a gas network connection (3.86% RH, 95% CI 2.31% to 5.41% RH) and the installation of new windows and doors (5.15% RH, 95% CI 3.73% to 6.57% RH) increased indoor RH levels. However, the increases were small in absolute terms. External wall insulation, which included the installation of mechanical ventilation, did not increase levels of indoor RH (–0.60% RH, 95% CI –2.26% to 1.06% RH) nor did the installation of boilers or heating systems (–1.59% RH, 95% CI –3.52% to –0.34% RH).

FIGURE 17.

Relative change in daily average indoor RH for different energy efficiency measures.

The effects of the intervention on indoor RH levels were different for different building construction types (Figure 18). The intervention increased indoor RH in buildings with cavity walls by 4.57% RH (95% CI 2.94% to 6.20% RH). The intervention decreased indoor RH levels in buildings with solid walls (–0.90% RH, 95% CI –1.76% to –0.03% RH). The intervention did not change indoor RH levels in British steel-framed buildings (–0.35% RH, 95% CI –1.49% to 0.78% RH).

FIGURE 18.

Relative change in daily average indoor RH for different construction types.

Duration and cumulative substandard internal conditions

The study further explored the impact of the intervention on the average daily duration and cumulative substandard internal conditions. Figure 19 shows that there is no evidence that the intervention reduced the daily duration of temperatures of < 18 °C (0.27 hours, 95% CI –0.49 to 0.96 hours) or <16 °C (0.20 hours, 95% CI –0.48 to 0.88 hours). However, the intervention did reduce the duration of indoor RH levels of > 60% RH by 1.14 hours (95% CI –2.00 to –0.28 hours).

FIGURE 19.

Relative change in daily average duration of substandard internal conditions for the intervention households.

Figure 20 shows that the intervention had a positive effect on the three cumulative substandard internal conditions measures. The cumulative amount of indoor air temperature of < 18 °C was reduced by 3.62 °C·hour (95% CI –6.95 to –0.30 °C·hour). The cumulative amount of the indoor air temperature of < 16 °C was reduced by 4.20 °C·hour (95% CI –6.64 to –1.76 °C·hour). The cumulative amount of the indoor RH levels of > 60% was reduced by 19.32% RH·hour (95% CI –29.68% to –8.96% RH·hour).

FIGURE 20.

Relative change in daily average cumulative substandard internal conditions for the intervention households.

Average daily gas usage

Figure 21 shows the average daily gas usage for the intervention (n = 26) and control households (n = 37) at baseline and follow-up periods. The calculation excluded the households from the off-gas areas for which no gas meter readings could be taken. Average daily gas usage decreased from 3.88 m³ to 2.45 m³ in the intervention households, a decrease of 36.9%. In contrast, the average daily gas usage increased from 4.60 m³ to 4.76 m³ in the control households. Having controlled by individual household heating demand, a repeated measures ANOVA showed that the intervention group × measurement occasion interaction was significant [F(1,60) = 35.985; p = 0.000; η² = 0.379 (Cohen’s d = 1.41)].

FIGURE 21.

Daily average gas consumption for the intervention and the control households at baseline and follow-up.

Key results

This study provided new evidence on the impact of energy efficiency investments on internal conditions and household energy use through detailed long-term household monitoring. Internal conditions were monitored for a minimum of 28 consecutive days before and after the installation of energy efficiency measures. These were compared with the internal conditions of households that did not receive such measures. The study found that the intervention raised indoor air temperature by an average of 0.84 °C, whereas average daily gas usage dropped by 37%. Similar increases were observed across different heating demand conditions. Furthermore, the intervention reduced the cumulative amount of the indoor air temperature that was substandard. Overall, the intervention did not increase indoor RH levels, although small increases were found for some individual measures. The study found that the intervention reduced the average daily duration and cumulative amount of indoor levels of > 60% RH.

The intervention measures were not equally effective. External wall insulation and connection to the gas mains network significantly increased indoor air temperatures; new windows and doors or a new heating system did not significantly increase indoor air temperatures. The increases in indoor air temperatures in British steel-framed buildings and buildings with solid walls could largely be attributed to the external wall insulation they received. Both new windows and doors and connection to the gas mains network increased indoor RH, although these increases were small in absolute terms. External wall insulation probably did not increase indoor RH because of mechanical ventilation. Increases in indoor RH levels were observed only in buildings with cavity walls, and not in British steel-framed buildings or buildings with solid walls. It shows the importance of using mechanical ventilation when making buildings more airtight. 64

The observed changes in indoor conditions were similar to or somewhat smaller than those found in previous research. The results of these studies are discussed in Chapter 1. However, in order to be able to compare different studies, changes in indoor conditions need to be accompanied by data on energy use. The extent to which the benefits of improved energy efficiency are taken as energy saving or as extra warmth can then be assessed. The latter is also known as the rebound effect. 133,134

Limitations

Although the study involved detailed long-term monitoring before and after the intervention, included a control group and controlled for external hydrothermal conditions, it did not monitor occupancy, heating or occupant behaviour. Occupancy and occupant behaviour have a large impact on the energy consumption and internal conditions of buildings. Including these aspects would improve our understanding of adaptive behaviours resulting from the energy efficiency investments. However, it was beyond the scope of the study to incorporate internal household dynamics into the research. The research uses estimates from meter readings made at the installation and collection of the monitors. This can only provide an indication of the energy savings as a result of the energy efficiency investments. Higher-resolution energy monitoring would allow the energy usage to be attributed to specific purposes and to provide information on occupancy and occupant behaviour.

Limitations regarding the sample are similar to the community-based study, from which participating households were recruited. These limitations are discussed in Chapter 3. The final sample of intervention and control households, however, were largely comparable, and the study had relatively low attrition. Although the study involved only a relatively small number of houses, they were observed for a minimum of 4 weeks before and after the intervention, resulting in a detailed data set with > 15,000 data points. The longitudinal study therefore allowed the model parameters to be estimated with far more precision, using 28–231 observations per household as opposed to just one.

The intervention involved a number of different energy efficiency measures, depending on the type and location of the properties. Although this means that the houses were non-identical and that the intervention differed across the different schemes, it allowed the study to estimate the effects of different energy efficiency measures in different types of buildings.

Interpretation

The study suggests that the intervention successfully increased indoor air temperatures. Although the overall increase was relatively small (in the order of 1.0–1.5 °C), it reflects long-term average increases, reducing the potential exposure of substandard temperatures: it brought the majority of indoor temperatures within the ‘healthy’ comfort zone of 18–24 °C. 124,125 An above-average increase in bedroom temperature suggests that the intervention helped to expand comfortable space within the home. 61 There is no evidence that insulation substantially increases indoor RH levels when accompanied by mechanical ventilation. This suggests that energy efficiency investment programmes such as Arbed will be beneficial primarily by providing improved living conditions that are conducive to good physical and mental health. 54 The reduction in gas usage suggests that the intervention has been successful in reducing financial pressure and improving living conditions in households in low-income areas, which were the main aims of the intervention programme.

Generalisability

The study involved detailed long-term household monitoring of a number of different households receiving a range of different energy efficiency measures through the intervention programme. There is little evidence that selection and attrition have systematically biased the sample, suggesting that the results may be generalised to similar energy performance investment programmes, as may the results regarding the specific measures and construction types. However, the results may not be directly generalisable to non-deprived communities or households with different financial circumstances, occupancy or heating patterns.

Economic studies for public health

Health economic analyses take many forms but can be broadly classified into two categories: cost studies and economic evaluations. A short description of the different types of cost studies and economic evaluations is provided in Box 1. The difference between the two categories is that cost studies focus on the identification of resources, impact and costs related to providing interventions and any cost offsets that may arise, whereas economic evaluation studies are comparative analyses that take account of both costs and benefits of the intervention and a comparator.

Previous economic studies of the health impact of housing improvement

A number of cost studies and economic evaluations have been conducted to assess the health-related quality of life and economic impacts of housing improvements. In a recent review of the literature, Fenwick et al. 74 identified 45 health economic studies relating to the health impacts of housing. It is clear from the review that only a limited number of health economic evaluations had been conducted during the period considered. Out of the 45 health economic studies, 29 reported cost and/or economic analysis and the majority involved cost studies (n = 25). Only four studies involved an economic analysis, although, in the opinion of the authors, 11 of the reported cost studies had sufficient data to conduct an economic evaluation. 74 Three studies stated that a CBA had been conducted but in fact it had not, and only one study was found to have conducted a CEA. Barton et al. 51 used the SF-36 to capture change in the health-related quality of life of residents as the basis for the economic evaluation. They concluded that the housing improvements did not produce substantial gains in terms of health-related quality of life, health or more schooling. However, they also recognised that there may have been insufficient time for measurable benefits to have materialised.

In addition to the studies reported by Fenwick et al. ,74 a small number of more-recent health economic studies have been conducted. The Gentoo social housing and sustainability group conducted a pilot study140 (n = 12) examining the health economic impact of energy efficiency improvements on people with COPD. The study found that self-reported GP appointments were reduced by 60%, accident and emergency (A&E) attendances by 30%, outpatient appointments by 22% and emergency admissions by 25%. The Warm Homes for Health project141,142 involved similar improvements, mainly focused on heating and insulation. The study suggests that installation of housing improvements produced cost savings to the NHS worth > £50,000. This would equate to an annual saving of £1B if all 4.8 million substandard homes in the UK receive the same energy efficiency measures. However, these two studies are at an early stage and at the time of writing the full results of their final health economic analyses have not yet been published.

Lawson et al. 143 conducted a CUA of a transfer of social and private tenants to new-build social housing rather than regeneration of existing housing stock. The study did not find a significant change in outcomes expressed as utility scores in the intervention group in comparison to a control group over a 2-year period. As a result, they concluded that the intervention was not value for money in health terms, although this was qualified by noting that not all benefits may have been captured and that they may not have been fully realised over the period of the study. 143

The research reported here builds on these prior studies but extends the body of evidence by using routinely collected health data in addition to self-reported survey data. The use of routinely collected health data allowed the intervention to be evaluated retrospectively using actual health-care utilisation data from the SAIL databank. 82–84,144 The study focuses on utilisation of secondary health-care services, including emergency admissions and contacts with primary care within NHS Wales, by people living in homes that received the intervention.

Study design

The health outcomes utilised in the economic analyses are based on the analyses undertaken using routinely collected data held within the SAIL databank. The methods used for these analyses are described in Chapter 2. Based on a literature review and the recommendations of NICE, CCA was considered to be the most appropriate methodological approach for the evaluation as it allows for different types of outcome to be considered. The CCA considers resource use and the related cost impacts of the intervention and benefits of different kinds to be considered and to be reported in a disaggregated form. Health service impacts and costs are thus considered as separate items to enable decision-makers to determine if the intervention represents good value from their perspective.

In addition to the CCA, a CUA was considered as an approach to evaluate the intervention programme. The CUA approach attaches utility values (the ‘Q’ value in QALYs) over time for study outcomes to provide one single measure (i.e. QALYs). The CUA considers resource use and cost impacts of the intervention and the benefits in terms of QALYs to be established for the intervention. In CUA, the intervention outcomes and the overall costs are compared with the relevant comparator. The intervention can ‘dominate’ the control (greater effect/lower cost), in which case it will be unambiguously cost-effective, or, in the event of a non-dominance (greater effect/higher cost), results are reported in the form of an incremental cost-effectiveness ratio (ICER) showing the additional cost per QALY gained.

A simple CUA based on QALYs derived from SF-12 responses is reported in Chapter 3. However, the utility values collected in the community-based study did not represent specific health states; rather, they were valuations of health experienced before and after the intervention was completed.

The economic analyses utilise the outcomes from the SAIL databank analyses described in Chapter 2, and follow a panel analysis approach utilising data available for the study population in the SAIL databank. The data were extracted for the study populations in monthly increments and used to develop a retrospective analysis (see Chapter 2). To fully utilise the SAIL databank outcomes, we looked to the literature and prior research to identify utility values for the health states experienced by individuals experiencing COPD-related emergency admissions.

The overall study period is 10 years, from 2005 to 2014. The intervention was delivered in 2010/11. Information collected prior to the intervention was utilised as a baseline to observe any subsequent changes in hospital admissions. The time horizon for the economic evaluation was 4 years post intervention.

As described in Chapter 2, the intervention programme included external wall insulation, boiler upgrades and replacements, microgeneration (photovoltaics/solar hot water/heat pumps) and general energy-saving advice. The lifespans of the different elements range from 12 years for boiler upgrades and replacements to 42 years for insulation (see Table 14). 91 Considering that the shortest lifespan of an element was 12 years, residents remaining in the property after the improvements will have benefited from the elements installed. Extrapolating beyond the study period seems inappropriate for the base case scenario, given the uncertainty about the health benefits that remain with an individual if they move out of properties over time. We believe that the 4-year time horizon of the study is appropriate and generalisable. To explore this element of uncertainty further, we undertook a sensitivity analysis, using threshold analysis to explore a range of durations of residency. We assumed that the impact was constant and the benefit continued after the observed study period. As the follow-up period after the intervention was completed was longer than 12 months, the costs and benefits beyond 1 year were discounted at a standard rate for public health interventions, currently 3.5%, to bring them into 2013 prices and a sensitivity analysis with 1.5%. 139

Setting

The economic analysis focused on the first phase of the intervention programme that took place in 2010 and 2011, in which a total of £68M was invested, including leveraged funding. The programme improved the energy efficiency of existing homes in low-income areas. LAs and RSLs submitted project plans to improve thermal efficiency of homes in Wales. The majority of homes were social housing. This study was undertaken using data for the intervention group providing their own historical controls. Individually reported baseline and follow-up periods in the intervention cohort were used to calculate the duration of the intervention for each resident and/or household.

Participants

The study participants within this study were individuals who lived within one of the intervention or comparator homes during the period under consideration. Anonymised housing codes were used to link the homes and individuals within the SAIL databank. All individuals who were a resident within a study home for ≥ 60 days were included in the analysis. Baseline data were collected for several years prior to the intervention.

Variables

A range of explanatory variables was collected for each individual and/or household. The variables utilised within this study were chosen for their theoretical power in explaining the levels of emergency admissions experienced. Information was collected at the individual level for age (in 5-year bands), sex and comorbidity (0, 1). Housing-level data were collected for area income deprivation (ordinal scale) and a measure of rurality (urban or rural). Given the seasonal trend observed within the dependent variables, an identifier for seasonality was also included. All outcome variables were grouped into the composite count measure of cardiovascular and respiratory emergency hospital admissions. To account for the variability in the duration over which individuals were observed, each of the count measures is transformed into a yearly rate. Data for each of these emergency admission variables were collected from PEDW. The PEDW data are structured into ICD-10 diagnosis chapters, described in Chapter 2.

Economic analysis

Two types of economic analysis were conducted: CCA and CUA.

Cost–utility analysis

We developed the event profile for COPD-related emergency hospital admission based on a structured literature review (see Appendix 12 and the search strategy reported in Appendix 13). The decline and partial recovery profile that characterises a COPD exacerbation was modelled to include five distinct phases as described by Seemungal et al. 150

The baseline utility value was sourced from a systematic review151 that reported UK-based utility scores derived from the EuroQol-5 Dimensions (EQ-5D) instrument for each of the four international severity levels for COPD. 152 The distribution of COPD in UK general practice using the Global Initiative for Chronic Obstructive Lung Disease (GOLD) classification was described in a study by Haughney et al. ,153 in which the combination of the EQ-5D and weighting data provided the baseline COPD utility. The GOLD stages represent varying forced expiratory volumes (FEVs). The baseline COPD utility score represents the value that individuals with COPD experience before an exacerbation occurs, whether severe enough to cause a hospital admission or otherwise. Table 16 reports the combination of the distribution of GOLD COPD stages and the utility scores representing the valuation of the health state. The resulting weighted baseline value was a utility score of 0.750.

TABLE 16 - The utility scores for COPD GOLD stages

GOLD stage of COPD	Distribution of COPD population (%)	Utility score
1	17.1	0.806
2	52.2	0.767
3	25.5	0.704
4	5.2	0.616

An emergency hospitalisation attributable to an exacerbation of COPD represents a detrimental impact on an individual’s short-term and possibly long-term health-related quality of life, represented here by health state utility scores. The literature search identified three papers that included utility valuations for individuals on admission and on discharge from a hospital stay for a COPD admission. 154–156 The utility scores for use in this analysis were created using a weighted average of all those reported in these papers, taking into account the number of individuals that the publication reported. Table 17 shows the number of individuals, utility value and publication from which the value was derived. The average utility score, derived from the literature for the COPD patients who experienced a hospital stay, is 0.504.

TABLE 17 - Reported utility valuations for individuals on admission and on discharge from a hospital stay for a COPD admission

Research paper	Number of patients	Utility value
Esteban et al.157	1421	0.600
Menn et al.155	117	0.446
O’Reilly et al.156	222	–0.077
Average		0.504

The COPD events that are serious enough to require hospital admission carry a risk of mortality. To account for this within this model, an inflated relative mortality measure was calculated. The data on COPD hospital admission mortality come from Esteban et al. 157 Given the average hospital stay duration of 7 days, all-cause mortality for this duration provides a baseline rate. The average age of patients in the literature was 72.6 years, whereas the data for COPD events utilised within this analysis show a mean age of 69.2 years. The relative all-cause mortality for these two ages was used to deflate the mortality observed in the literature to a rate representative of COPD hospitalisations for the data used in our analysis. The all-cause mortality was calculated to be 0.031% for the 7-day period, whereas those experiencing a COPD-related hospitalisation had a mortality rate calculated to be 2.507%. The net increase in mortality attributable to COPD hospitalisation is 2.476%. Taking into account this increased mortality when estimating the utility value for a COPD admission for an exacerbation, we estimated a utility value of 0.492.

The estimation of a discharge utility score follows the same approach as estimating the admission value. Hospital discharge values were obtained from the same three papers as the admission figures. 155–157 The data sourced from the literature report 1289 individuals with a mortality-adjusted average utility score of 0.613. As previously mentioned, COPD events are characterised by an initially large reduction of health-related quality of life followed by a recovery phase to prior health. However, some individuals may ultimately never fully recover to the same health and FEV levels they had prior to the exacerbation.

The post-discharge recovery phase was estimated using the recovery statistics reported by Seemungal et al. 150 The duration of an event that began with a hospitalisation attributable to COPD was estimated by Seemungal et al. 150 to be a total of 91 days. Given a 7-day hospital stay, the remaining 84 days are characterised by two phases: first, 28 days following discharge, during which 75.2% of individuals were found to make a full recovery; and, second, the subsequent 56 days, during which 79.8% of those remaining not fully recovered were reported as still experiencing a negative residual impact of their event. The utility score of these two recovery points is calculated according to the percentage of individuals recovering from the discharge utility value back to the initial baseline value. The utility score for individuals 28 days post discharge was calculated as 0.720, increasing to 0.726 at 84 days. The figure of 0.726 is assumed to be the long-term utility score.

Figure 22 plots the five COPD health states and the related utility values, illustrating the sharp decline caused by the hospitalised exacerbation event followed by the gradual recovery that ultimately never reaches the initial baseline value. The area under the curve approach was used to estimate the short- and long-term reduction in QALYs. The short-term calculation assumes that the hospitalisation occurs in the middle of the year with a within-year QALY reduction of 0.022. The long-term impact of a COPD event is a reduction of 0.240 QALYs.

FIGURE 22.

Time course and utility values for a COPD exacerbation event.

Although commonly used for estimating health valuation over time, utility decrements may fail to account for the full detrimental impact of a COPD event when used to estimate a structured event pathway for a COPD patient. Rutten-van Mölken et al. 158 sought to capture the broader holistic impact of a serious COPD exacerbation using an isolated time trade-off valuation approach. This time trade-off study estimated a single serious exacerbation to reduce health state utility by 0.042. This study viewed an event within the context of 1 year as opposed to the modelling undertaken in this analysis. The extended time frame obtained from the five-point calculation aligns well with the panel data analysis in that it accounts for the longer-term impact of reductions in FEV.

To inform our CUA and economic model, each adverse health event resulting in a hospital admission had a curve mapped from the utility values across the study period. This approach incorporates the initial impact of the event and a time-variable component. The analysis utilised cost associated with the intervention and the improved health following a reduction in COPD events to generate an ICER. 159

Cost–consequence analysis

The CCA outcomes are presented in Table 18. The outcomes for the primary objective are reported separately from the costs. The average change in emergency admissions by year is weighted according to the prevalence levels within each of the 4 post-intervention years. Table 18 reports the primary objective alongside the intervention costs. The costs and outcomes are discounted to present-day values at 3.5%.

Table 18 reports four data columns and totals. The ‘weighting’ column offers the calculation needed to transform the overall impact into a yearly value, which is based on the prevalence of the measure in each year. The change in admissions (B) and SD are reported in the second data column; the fourth data column reports the discounted effects and attached treatment costs. The third column includes the cost of the intervention, which is combined with the changes in treatment costs to offer the final cost component. The total effect value is a simple summation of the four yearly changes in admissions.

The results suggest a non-significant increase in hospital admissions for the primary outcome: over the 4 years, the cumulative impact is 0.0041 events per person. The per-person cost over the post-intervention period amounts to £345.75, which is driven by an intervention cost of £334.44 and an increase in treatment costs of £11.31. Given the increase in the primary outcome following the intervention and the positive intervention costs, the intervention is not deemed as cost-effective.

The results using the secondary outcomes are reported in Tables 19–21. The approach is the same as with the primary outcome but leaves out the intervention costs. The intervention costs are not included in the tables to avoid double counting. Table 22 reports the combined outcomes and costs for the four measures.

Table 19 reports the impact on the COPD-related hospital admissions per person. The reduction in COPD emergency admissions is not significant at a 95% confidence value; the summation of these event reductions over the 4 years totals to –0.0006 per person. The scale of this reduction is very small and suggests a reduction in NHS treatment costs of £1.64. The reduction of 0.0006 events should be considered alongside each of the following impacts. The weighting levels in Table 20 show that COPD events were increasing over the 4-year period.

Table 20 reports the impact on the cardiovascular-related emergency hospital admission events per person. As with the COPD results, the cardiovascular event levels have reduced non-significantly. The scale of the reduction is 0.0053 and the discounted amount saved is £14.56. The first year following the intervention saw the lowest levels of cardiovascular emergency admissions.

Table 21 reports the impact on the respiratory-related emergency admission events per person. The respiratory emergency admission event changes following the intervention are positive but do not achieve statistical significance. However, the scale is much greater than that for either the COPD or the cardiovascular results. Given that the overall respiratory and cardiovascular findings show an increase in frequency, the two relatively small decreases and the finding that one component was positive and dominating are not surprising.

The combinations of each of the secondary outcome measures alongside the intervention costs are reported in Table 22. The intervention reduces COPD and cardiovascular emergency admissions but increases the number of respiratory-related admissions. This is at a net cost of £248.48 per person over a 4-year period.

Cost–utility analysis

The CUA utilises the data from the CCA and develops the analysis further into an economic evaluation using the data identified in the literature review (reported in Appendix 12). Our analysis suggests that a within-year QALY decrease for a single COPD exacerbation hospital admission is 0.022. The residual decrement to utility scores in subsequent years after the initial year of the event results in a reduction in QALYs of 0.024. The inclusion of these QALY valuations in the 4-year model is presented in Table 23.

The relatively small decrease in COPD events and the relatively large cost of the intervention programme mean that the ICER is > £10M (£10,485,472.12) per QALY gained. When using a discount rate of 1.5% instead of the base case 3.5%, the ICER reduced to £10,066,540.29. Both of these ICERs are deemed not cost-effective.

Threshold analysis was undertaken to estimate the required reduction in COPD events and related utility scores over the 4-year period to make the intervention cost-effective. The base-case analysis estimates suggest that the intervention is not cost-effective, as it would require a constant yearly per-person reduction in utilities associated with COPD events of 0.028 in order to make the intervention appealing in terms of a cost per incremental QALY gained of £20,000–30,000. Given the long-term investment associated with the intervention, a 10-year threshold analysis was estimated. The benefits of the cumulative health-related quality-of-life benefits require a yearly decrease in utility scores of 0.013 for the intervention to be considered cost-effective. The disparity between these two figures highlights the influence of the duration of analysis. With a condition such as COPD, which has a long-term decrement to health-related quality of life, interventions that deliver benefits consistently over an extended period may be perceived more favourably with extended timelines. Given the relative scale of the required benefits estimated by the threshold analysis in the shorter term compared with those reported in Table 23, time horizons of > 10 years were not investigated.

The PSA varied the yearly reductions in COPD admissions alongside a uniformly distributed cost of intervention. The 1000 replications are plotted on a CEP (Figure 23). Given the scale of reduction observed in the statistical analysis and the costs involved, it is important to note the axis units. The QALY axis reports numbers in the thousandths of a QALY whereas the net cost unit is in hundreds of pounds. The impact of the intervention on COPD events has a 0% chance of the intervention being cost-effective at a £30,000 per incremental QALY gained level. The CEAC is not illustrated owing to the lack of movement at plausible ICERs.

FIGURE 23.

Probabilistic sensitivity analysis results on a CEP.

The findings reinforce the uncertainty surrounding the statistical outcomes and highlight the relatively small scale of the impact on COPD event rates in comparison with the intervention costs. The furthest outlier in favour of the intervention saves 0.004 QALYs at a cost of £314.14.

The PSA estimations are also reported as a CEAC in Figure 24. The relatively small-scale impact on the effectiveness of the intervention in terms of improvement of utility scores and relatively high costs of the intervention resulted in a 0% chance of cost-effectiveness using a threshold of £30,000 per QALY gained. The scale of the CEAC relates to the relative cost and effectiveness levels and provides an illustration of the positions where the likelihood of cost-effectiveness changes. The upper left-hand quadrant of the CEP in Figure 23 shows the occurrence of dominated observations (higher costs and worse health outcome), which accounts for 36.1% of the estimations. The maximum percentage of estimations that could be considered cost-effective (i.e. < £30,00 per QALY gained) is 65.9%; the CEAC illustrates up to 54% of these.

FIGURE 24.

Cost-effectiveness acceptability curve for the intervention.

Key results

As with all economic evaluations, the outcomes of the analyses are driven by the effects of an intervention as well as the costs. In the case of this analysis, the costs incurred by the intervention are large, overwhelming the benefits. The disaggregated outcomes derived from the intervention were balanced against the costs in the CCA. As shown in Chapter 2, the change in emergency admissions following the intervention was non-significant. This could be interpreted to mean that the investments, whether the lower bottom-up or the higher top-down reported cost, have not delivered identifiable health benefits in terms of reduced costs to the health service. Similarly, in the CUA, which explored the impacts of the intervention on QALYs relating to the change in rate of emergency admissions for people with COPD, the small, non-significant reduction in emergency admissions is overpowered by the cost of the intervention. Therefore, the intervention cannot be considered cost-effective using commonly accepted norms, with or without discounting costs and benefits to present-day values in line with best practice. It is important to consider that this does not mean that the intervention is without benefit, but rather it may be that the benefits were not able to be identified and measured through the approaches we utilised.

Strengths and limitations

A strength of the current study was the use of routine data held within the SAIL databank. Unlike other health economic studies that focused on affordable warmth interventions, this study was able to use actual health-care utilisation data with near-complete data for the study population (see Chapter 2). However, the data set will have included people with a wide range of health problems of different stages of severity and no information was available regarding the initial quality of housing and, therefore, the relative improvement resulting from the intervention.

Another strength of the study was that data were used from both the data linkage and the community-based field study. Although routine data allow calculations to be based on actual health-care utilisation, emergency hospital admissions are only a proxy measure for health status. This type of contact with the health-care system can provide a signal that health is changing but will only be one part of the overall story. The community-based field study provided a more detailed understanding of the health, well-being and health-related quality-of-life impact of the intervention, and was used as a basis for a CUA. The results of that analysis are reported in Chapter 3.

It was not possible to undertake a CBA, an approach recommended by NICE as an option for evaluating public health interventions, because the available data did not facilitate identification and valuation of all of the impacts of the intervention to society and the full societal cost and consequences of the intervention. It could be useful to conduct such analyses in the future, considering that a housing intervention is likely to have a wide range of benefits beyond health improvements alone. The community-based study showed that the intervention provided a wide range of psychosocial and economic benefits to residents. It is recognised by NICE, however, that CBA poses challenges in terms of obtaining all necessary data to undertake analysis. It was beyond the scope of the study to value these benefits.

We explored the impact of the intervention for up to 10 years (i.e. the probable lifespan of the shortest-lived elements of the intervention), but the effects of the intervention are plausibly longer. A study using longer-term data and a longer-term time horizon may deliver different results.

Interpretation

When trying to determine whether or not an intervention delivers good value for money, the intervention does not necessarily have to be cost-sparing or cost-effective in terms of what would be acceptable for a clinical intervention. Public health decision-makers and budget holders may feel that the goals of the intervention – in this case the delivery of affordable warmth, alleviation of fuel poverty and reduction of CO₂ emissions – justify the costs of the intervention. The fact that our economic analysis suggests that the intervention incurred major costs but did not lead to detectable cost reductions to the health service or improvements in QALYs for people with COPD does not mean that the intervention is without benefit. Indeed, the community-based study showed that the intervention provided a range of social benefits and made it easier and cheaper for households in low-income areas to heat their homes. In addition, the health benefits may emerge over a longer period than the 4-year horizon used in this study, especially as a prevention intervention. A child growing up in a property may not have health impairments that he or she may otherwise have had without the improvements.

The Gentoo140 and Warm Homes for Health studies,141 which found health improvements and cost savings after housing improvements, were studies that targeted people with poor housing and the capacity to benefit healthwise. The CUA undertaken with the COPD subpopulation may have been limited by a similar problem. COPD that is sufficiently severe enough to present a risk of hospital admission is defined as moderate to severe. 160 People with moderate to severe COPD are prone to frequent exacerbations (three or more exacerbations per year is part of the definition) and these are an important cause of hospital admission and readmission and, therefore, have a considerable impact on health-related quality of life and daily activities. 150 Reducing exacerbation frequency through improved housing for these people might be more valuable than for others with less-severe COPD, and might spare more health-care resources. However, a hospital admission may be precipitated by a lack of social support and comorbidities rather than severity, which our study data were not able to reveal, but an exacerbation avoided by someone who might fall into this category may have additional value. Focusing an analysis on all such patients may reveal a different picture to the one our present analysis suggests.

Generalisability

This economic study and our findings would be generalisable to a developed country in a temperate region where a national health service exists founded on the principles of solidarity and tax-funded health care.

The community-based study and the reconvened focus groups

The community-based study found no evidence that the improvements in energy efficiency lead to better mental and physical health in the short term. The intervention was associated with neither improvements in key mental and physical health outcomes nor changes in self-reported respiratory and asthma-related symptoms. However, quantitative evidence was found that the intervention led to improved subjective well-being during the study period, as well as to improvements in a number of psychosocial outcomes that may be part of pathways to better health. This included increased thermal satisfaction, fewer reported financial difficulties, increased satisfaction among participants with the repair of their homes, fewer reported housing-related problems and more social interactions.

These findings were reflected in the focus group discussions that were conducted as part of the resident engagement. The longitudinal focus groups showed the importance of improving the energy efficiency of houses in low-income neighbourhoods. 161 According to residents, the intervention made a great difference to the comfort and warmth of their homes, opened up spaces within the home and reduced their heating bills substantially. This not only helped to relieve financial stress and fuel poverty but made them feel less socially isolated. This confirms that the benefits of the improvements were, at least in the short term, more closely linked to better well-being owing to improved socioeconomic conditions than to physical health outcomes. Experiences with the delivery of the intervention were mixed, which some residents found disempowering and stressful.

The household monitoring study

The household monitoring study demonstrated that the improvements in energy efficiency raised indoor air temperatures and helped households to reduce their energy use. The increase in air temperature was consistent across different heating demand conditions. Although no evidence was found that the intervention reduced the duration of substandard temperatures within the homes, there was a small decrease in the cumulative amount of substandard temperatures (i.e. the time intensity integral of substandard temperatures). However, this reduction was small in absolute terms.

The different energy efficiency measures were not equally effective in raising indoor air temperatures. External wall insulation and connection to the gas mains network were the most effective, whereas new windows and doors or a new heating system did not lead to significant changes in indoor air temperature. The greatest increases in indoor air temperatures were found in British steel-framed (BISF) buildings and buildings with solid walls, which had the lowest energy performance ratings before the intervention. That indoor air temperatures increased most in the evening and at night, as well as in the living room and main bedroom, suggests that the intervention makes the biggest difference when spaces are in use.

Overall, no evidence was found that the intervention increased indoor RH levels. However, some evidence was found that the intervention decreased the duration and cumulative amount of substandard temperatures. Although no evidence was found that the intervention increased indoor RH levels overall, some evidence indicated that individual measures did. Both a connection to the gas mains network and the installation of new windows and doors were associated with small increases in indoor RH levels. However, the increases were small in absolute terms.

The data linkage study

The data linkage study found no evidence that the intervention reduced emergency admissions for either the primary outcome (combined cardiorespiratory emergency hospital admissions) or most secondary outcomes (emergency hospital admissions for cardiovascular, respiratory and COPD conditions, and excess winter admissions) for people of all ages living in an intervention home. The study also did not find evidence of a significant intervention effect on our primary outcome when focused only on residents aged ≥ 60 years at the mid-point of their residence in an intervention home. However, the study did find a statistically significant intervention effect on cardiovascular-related emergency admissions: there was an increase in emergency cardiovascular admissions post intervention for those aged ≥ 60 years. Although we controlled for age in our analyses, it is possible our analyses have not taken all effects of ageing into account. It may be that age does not have a linear response and the older people in this group are increasingly frail, having had poor health conditions set in motion at an earlier age, working to outweigh the potential for reduced admissions as a result of a single thermal efficiency intervention.

The economic evaluation

The CCA undertaken as part of the economic analysis did not find evidence that the intervention delivered explicit reductions in cardiorespiratory-related emergency admissions. The costs of achieving this outcome relate to the costs of delivering the intervention unmodified by savings in emergency admissions. However, the purpose of undertaking CCA is to present costs and benefits separately, allowing the reader or decision-maker to make their own decision about the relative value of the benefits compared with the costs. As reported previously, there were social benefits from the intervention, albeit not demonstrably seen in emergency admissions. The increased warmth and well-being derived from housing improvements may well be considered worthwhile irrespective of the impact on health-care activity.

The CUA explored, through modelling methods, the impact on QALYs of the change in rate of emergency admissions for people with COPD. However, the impact on COPD-related emergency admissions is overpowered by the cost of the intervention and, therefore, cannot be thought of as cost-effective using commonly accepted norms.

Round 1: before installation (2014)

Round 2: after installation (2015)

Data items

The data items extracted included the following: author, year, country of origin (data), sample size, age, sex, COPD GOLD stage/severity level, study type, time of measurement of EQ-5D, data source, EQ-5D tariff value and HSUVs. Risk of bias was assessed at outcome level only. The primary outcome was HSUV.

Overview of all health state utility values studies for patients with chronic obstructive pulmonary disease

After the initial search, 79 studies were identified to include HSUVs for patients with COPD. The studies incorporated data from the UK, Spain, France, the Netherlands, Germany, Switzerland, Italy, Norway, Sweden, Turkey, Brazil, China, the USA and Canada. In addition, several studies involved multicountry data sets in which individual countries were not identified. 210,273

The majority of studies reported HSUVs based on the EQ-5D (73 studies154–156,158,173,174,177–179,184,187,191,193,194,197,200–202,205–213,216,218–222,225–227,229,231,232,235–237,239,240,242,244–246,248,250,252–254,260–262,265,269,271,273,275,276,279,285,288,292,294,297,301–304,306); some studies also reported utility values based on the SF-36/SF-12/SF-6D (nine studies155,173,182,258,288,297,299,303,306). In addition, one study used HUI,305 one study used QWB307 and one study used the 15-dimensional measure of health-related quality of life. 303

Eighteen studies177,178,184,191,216,222,244–246,254,260,261,269,286,297,301,304,306 were UK based (UK data set or, if secondary data were used, UK lead authors), five studies included UK data in pooled analysis and 27 studies155,156,173,177,184,191,210,216,222,225,227,231,250,254,260–262,269,273,276,279,294,297,301–304 used UK tariff values. Not all studies explicitly stated the tariff values used so instead, when possible, this was deduced by the references used.

Although a large number of studies were identified, many used overlapping data sets that were not always initially obvious. For instance, modelling studies often used secondary data from the same clinical trials; for example, Eklund et al. 187 and Karabis et al. 235 used data from the UPLIFT trial. 308 Other studies also reported secondary data in other studies; for example, Wacker et al. 209 report data from Burns et al. 177 and Rutten-van Mölken et al. 210 report data from Wilson et al. 178 Many studies used pooled data from several trials; for example, Boland et al. 212 used pooled data from the Randomised Clinical Trial on Effectiveness of Integrated COPD Management in Primary Care (RECODE),175,176 the Assessment Of Going Home Under Early Assisted Discharge (GO-AHEAD) trial214 and the Health Status Guided COPD Care (MARCH) trial. 215 Other studies used data from the same national surveys for different and/or overlapping years; for example, Kwon et al. ,194,197 Lee et al. ,194,201 Hong et al. 194,218 and Kim et al. 194,219 use data from the Korean National Health and Nutrition Examination Survey (KNHANES). 199

The initial scan found three review papers with full-text availability in relation to COPD patients with stable COPD151,172,309 and the full search did not identify any additional reviews (Table 27).

Pickard et al. 309 estimated average HSUVs by disease severity based on pooled data from 1988 to 2007. Petrillo et al. 172 updated the search by Pickard et al. 309 and provided HSUV ranges by disease severity and a summary of the HSUV change during an exacerbation (community or hospital based). Moayeri et al. 151 conducted a meta-analysis on COPD HSUV studies that were published prior to 2014 using UK tariff values and produced average utilities by disease severity.

Change in health state utility values during a hospital admission for an exacerbation of chronic obstructive pulmonary disease

Three studies considered change in EQ-5D-generated HSUVs from hospital admission to discharge,154–156 two of which used UK tariff values. 155,156

There was large disparity in HSUVs between the studies using UK tariff values, particularly in relation to HSUVs on admission. For instance, mean admission and discharge HSUVs for O’Reilly et al. 156 were –0.077 and 0.576, respectively; whereas, for Menn et al. ,155 the reported weighted average admission and discharge HSUVs were 0.61 and 0.78, respectively. However, differences can be explained by the timing of the measurement; whereas patients in O’Reilly et al. 156 completed the EQ-5D ‘on admission’ (i.e. at the most severe part of their exacerbation), patients in Menn et al. 155 completed the EQ-5D ‘within 3 days after admission’ (i.e. after treatment had started, when it is likely symptoms had improved). Similarly, Esteban et al. 154 reported similar values (0.60 on admission and 0.64 on discharge) to those reported by Menn et al. ,155 when data were collected ‘on the first day after admission’, again after treatment had started (Table 28).

Residual effect on utility values after an admission to hospital with an exacerbation of chronic obstructive pulmonary disease

Five studies (Table 29) report the residual effect of EQ-5D-generated HSUVs after an exacerbation requiring hospital admission,156,158,246,252,253 three of which used the same data set. 158,246,252 The residual effect was tracked over three timescales: 3 months,156 12 months158 and a varied timescale related to previous exacerbation. 253 Only one study used UK tariff values. 156

Phenotype

Two studies reported utility values by phenotype, although each considered different subgroups. Mean utility values in each group ranged from 0.63 to 0.69 in Ding et al. 182 and from 0.52 to 0.69 in Miravittles et al. 220

Ding et al. 182 found patients with asthma–COPD overlap syndrome (ACOS) and asthma only to have the lowest HSUVs in comparison with COPD only (COPD, chronic bronchitis or emphysema) or controls (those without asthma, COPD, chronic bronchitis or emphysema). In contrast, Miravitlles et al. 220 studied a cohort of COPD patients and found the ‘excerbators with chronic bronchitis’ group to have the lowest HSUV in comparison with ‘excerbators without chronic bronchitis’, ACOS or ‘non-excerbators’.

Age

Four studies considered HSUV by age, with mean HSUV ranging from 0.42 to 0.94. 194,219,262,279,301 All studies showed a general trend towards a decrease in HSUV with age, with a slightly greater decrease seen in females than in males. 194,219,301 However, this sex difference is particularly pronounced in the South Korean study, which, as mentioned previously, has a high percentage of males, meaning differences may be exaggerated by a small female sample size. 194,219

Sex

Six studies reported sex differences in HSUV, with overall mean utility values ranging from 0.60 to 0.93. 191,194,219,225,236,262,279 Four out of six of the studies reported that females have a lower HSUV, with differences ranging from 0.03 to 0.11. 191,225 Two studies reported that males have a higher HSUV; however, both studies have male-dominated cohorts [Kim et al. 236 (91.5% male) and Kim et al. 194,219 (74.0% male)] and are based on a specific population (i.e. South Korean).

Number and severity of exacerbations

Two studies looked at HSUV by number of exacerbations, reporting a reduction in HSUV with an increasing number of exacerbations,221,279 and one study considered utility decrements by severity of exacerbations, reporting greater decrements in HSUVs with increasing severity. 158

Number and type of comorbidities

Three studies considered the effect of specific comorbidities on HSUV. 202,206,221 The greatest differences were found between those with and without depression. Both Martinez Rivera et al. 202 and Miravitlles et al. 206 found that patients with COPD and depression had a lower mean HSUV than patients with COPD only (0.40 and 0.55 vs. 0.76 and 0.83, respectively). Miravitlles et al. 221 also found that those with comorbid cardiovascular disease had a lower mean HSUV (0.78) than patients with COPD only (0.82); however, no differences were found for patients with and without diabetes, and patients with comorbid haematological malignancies had similar HSUVs.

One study measured HSUVs in relation to a number of comorbid diseases in patients with COPD and found that HSUV decreased as the number of comorbidities increased. 194,218 In addition, Miravitlles et al. 221 also considered HSUV in relation to the Charlson index, with mixed results: those scoring 0, 1 and 3 had similar utility scores (0.82, 0.82 and 0.81, respectively), whereas those scoring 2 had a lower HSUV of 0.74.

Smoking history

Three studies assessed smoking status in relation to HSUV in patients with COPD, with mixed results. The studies report smokers with HSUVs higher than,194,201 lower than242 and the same as221 non-smokers.

Body mass index

Two studies report BMI in relation to HSUV in patients with COPD, with mixed results. 221,232 The lowest HSUV was reported in underweight patients (0.69)221 and the highest in overweight patients (0.90);232 however, the general relationship between HSUV and weight was not linear.

Socioeconomic status

Two studies considered HSUV by socioeconomic status for patients with COPD, both reporting that HSUVs increase as socioeconomic status increases. 194,219,271