case control study research proposal

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• Published: 23 November 2020

Clinical Study

A case-control study to evaluate the impact of the breast screening programme on mortality in England

• Roberta Maroni   ORCID: orcid.org/0000-0001-6420-2881 1   na1 ,
• Nathalie J. Massat   ORCID: orcid.org/0000-0002-1095-994X 1   na1 ,
• Dharmishta Parmar 1 ,
• Amanda Dibden   ORCID: orcid.org/0000-0002-0599-9840 1 ,
• Jack Cuzick 1 ,
• Peter D. Sasieni   ORCID: orcid.org/0000-0003-1509-8744 2   na2 &
• Stephen W. Duffy   ORCID: orcid.org/0000-0003-4901-7922 1   na2  

British Journal of Cancer volume  124 ,  pages 736–743 ( 2021 ) Cite this article

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• Breast cancer
• Cancer screening

Over the past 30 years since the implementation of the National Health Service Breast Screening Programme, improvements in diagnostic techniques and treatments have led to the need for an up-to-date evaluation of its benefit on risk of death from breast cancer. An initial pilot case-control study in London indicated that attending mammography screening led to a mortality reduction of 39%.

Based on the same study protocol, an England-wide study was set up. Women aged 47–89 years who died of primary breast cancer in 2010 or 2011 were selected as cases (8288 cases). When possible, two controls were selected per case (15,202 controls) and were matched by date of birth and screening area.

Conditional logistic regressions showed a 38% reduction in breast cancer mortality after correcting for self-selection bias (OR 0.62, 95% CI 0.56–0.69) for women being screened at least once. Secondary analyses by age group, and time between last screen and breast cancer diagnosis were also performed.

Conclusions

According to this England-wide case-control study, mammography screening still plays an important role in lowering the risk of dying from breast cancer. Women aged 65 or over see a stronger and longer lasting benefit of screening compared to younger women.

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Following an evaluation of several randomised controlled trials (RCT) 1 that showed an overall reduction in mortality from breast cancer in women undergoing mammography screening, the National Health Service Breast Screening Programme (NHS BSP) was launched in the United Kingdom (UK) in 1988. At the time, it aimed to offer free routine screening to every woman aged 50–64 once every three years. It now invites women aged 50–70, with an age extension to younger and older women (47–73 years) being trialled. 2

Over the last thirty years, major advances have been made in the fields of cancer screening, treatment, and management (including effective adjuvant systemic therapies 3 and two-view mammography 3 , 4 ), with resulting lengthening of survival times after a breast cancer diagnosis. 5 Despite recent reductions in breast cancer mortality, breast cancer is still the cancer with the highest incidence 6 and the second most common cause of cancer death 7 in females in the UK.

Case-control studies are a useful tool to evaluate screening programmes in settings where lack of equipoise would mean that RCTs would be unethical, or as in this case, where the RCTs have already been done, but there remains a need to ensure that the service is delivering the expected clinical benefit. Case-control studies also overcome some limitations associated with other observational designs by taking into account changes in cancer incidence and use of treatments over time and adjusting for any imbalances in other factors that could affect breast cancer mortality.

Taking as an example a case-control study 8 that resulted in policy change within the NHS cervical screening programme by altering age at first screen and the screening interval, we designed a similar study focussing on the NHS BSP with the aim of:

Evaluating the effect of mammography screening in the NHSBSP on breast cancer mortality

Evaluating the effect of mammography screening on breast cancer incidence, and incidence of late stage disease

Estimating overdiagnosis

Analysing the interplay of early detection, pathology, and treatment on fatality of breast cancer.

The study protocol and results from two pilot studies have been published previously. 9 , 10 , 11 This paper reports on the first objective above (breast cancer mortality), making use of England-wide data. Effects on incidence etc. will be reported in future papers.

Definition of cases and controls

As the main objective was to evaluate the effect of mammography screening on breast cancer mortality, cases were defined as women whose primary cause of death was breast cancer, who were diagnosed at age 47 years or older and died at age 89 years or younger in 2010–2011. We chose the lower limit of 47 as there is a major trial of screening in ages 47–49 ongoing, 2 so substantial numbers of women have been screened in this age group. We chose the upper limit of 89 because above this age we would not expect a major effect of screening taking place mainly at ages 50–70, because we were less confident of the cause of death in the very old, and because screening is essentially aimed at preventing premature mortality, which one might reasonably interpret as death below age 90 years. Only diagnoses occurring after 1990 were included in the analysis. Their matched controls were women sampled from the general population of those invited for screening (99.9% of women eligible for screening in England 12 ) and alive at the time of their corresponding case’s death. Controls may have been diagnosed with breast cancer, but not before their case’s date of diagnosis. Where possible, two controls were selected per case and matched on date of birth (within one month of the case’s) and screening area at date of diagnosis.

For the purposes of the statistical analysis, controls were assigned a date of pseudodiagnosis, equal to the diagnosis date of their corresponding matched case. To be eligible as a case or a control, a woman had to have had at least one invitation to screening prior to the date of diagnosis/pseudodiagnosis.

The primary endpoint was to estimate, among those invited to breast screening, the effect of ever attending breast screening on mortality from breast cancer. Changes in this effect over time were also investigated. Secondary endpoints included the effect of measures of screening intensity, such as time between last screen and diagnosis/pseudodiagnosis, and their estimations in different age subgroups.

Data selection and linkage

Cases were identified from the National Cancer Registration and Analysis Service (NCRAS) database accessed through the Office for Data Release of Public Health England (PHE). This database contains Office for National Statistics date and cause of death data. NHS Digital used the National Health Application and Infrastructure Services (NHAIS) system to identify matched controls and provided breast and cervical screening histories within.

We excluded any breast screens occurring outside the usual call/recall system of the national screening programme. All the screening histories of the study subjects were considered up to and including their date of diagnosis/pseudodiagnosis.

The data were processed according to the NHS Information Governance guidelines. 13

Sample size

Sample size calculations for the pilot study showed that, assuming an OR for breast cancer mortality of 0.7 and a number of discordant pairs of 33%, two controls per case with 800 breast cancer deaths and 1600 controls would confer more than 90% power to detect such an effect size at the 5% significance level using a two-sided test. 10 As the data for this main phase encompassed the whole of England, we had ample power, not only for the primary outcome (8288 cases and 15,202 controls after exclusions), but also for subgroup analyses.

Statistical analysis

Data were analysed using Stata version 13 14 by matched (conditional) logistic regression with death from primary breast cancer as the outcome. Date of birth and screening area were accounted for by the matching process.

Ineligible subjects were excluded (see Fig.  1 ). For some of these, this resulted in a matched set containing only a case, or only controls, which could then no longer be used in the matched logistic regression. Sensitivity analyses using unmatched logistic regression and controlling for age at diagnosis/pseudodiagnosis and screening area were performed on the same dataset with fewer exclusions; in this case, the inclusion criteria considered were the same, but the fact that a case or a control was excluded did not imply discarding that matched set.

Asterisk indicates that these records were excluded for being in a 1:1 matched set where the case or the control was excluded or for being in a 1:2 matched set where the case or both controls were excluded. Hash indicates that these become 1:1 matched sets in the final dataset. Note: some records may be excluded for more than one reason.

Case-control studies used to evaluate population screening programmes are subject to a type of bias known as non-compliance or self-selection bias, which is based on the assumption that people who are already ill may be less likely to attend screening and those who do attend may be more health conscious, and therefore healthier, than those who do not take up the invitation. This may confer an artificially greater protective effect for screening, which was corrected in our analyses using a variant of the method by Duffy et al. 15

The effect of self-selection bias was estimated using data available on cervical screening attendance for the women in the study, on the basis that any observed protective effect of cervical screening on breast cancer death cannot be due to cervical screening (which does not include breast examination) and is therefore likely to be caused by self-selection bias. In particular, the odds ratio (OR) uncorrected for self-selection is an estimate of the relative risk:

An unbiased estimate of the effect of screening on risk of dying from breast cancer would be (refer to Duffy et al. 15 ):

The OR for death from breast cancer associated with attendance at cervical screening, i.e. the self-selection correction factor, can be considered an approximate estimate of the relative risk:

Therefore, we obtain an estimate of θ by dividing γ by φ . The fundamental assumption here is that the populations choosing to attend or not to attend cervical cancer screening have the same risk of dying of breast cancer a priori as those choosing or not choosing to attend breast cancer screening. We do not assume that the effects of self-selection are the same in the two programmes. This is referred to as our first method of correction in the Results section.

As there is considerable uncertainty in the extent of self-selection, and of course decisions to attend at two separate screening programmes are likely to be confounded with each other, we also corrected for this using the method of Duffy et al. 15 . This method estimates the effect of participation in screening in those who would participate if invited as:

where p is the proportion of the invited population who participate in screening and D r is the a priori relative risk of dying of breast cancer for someone who chooses not to attend compared to an uninvited general population member. We estimated D r as 1.19 (95% CI 1.11–1.27), from the cohort study of Johns et al. 16 Thus, this correction was based on a prospective estimate of the extent of self-selection bias in a cohort of 988,090 women in the NHS Breast Screening Programme. We estimated p as 73.4% from the annual report of the National Programme. 12 This method, referred to as our second method of correction in the Results section, also yields an estimate of the effect of invitation to screening as follows: 15

More details on the methods are available in the published study protocol 9 and pilot study analysis. 10

The study dataset had a total of 9550 cases and 17,993 controls. There were 1107 sets with matching ratio 1:1 (1 case to 1 control) and 8443 sets with matching ratio 1:2 (1 case to 2 controls). Records of 1262 cases and 2791 controls (15% of the total) were excluded for various reasons before the statistical analysis (see study flow diagram in Fig.  1 ). This left a final dataset of 8288 cases and 15,202 controls, divided into 1,374 matched sets of size 1:1 and 6914 of size 1:2.

Sensitivity analyses using unconditional logistic regression were performed including subjects without a matched case or control, leaving us with 8479 cases and 16,794 controls.

Table  1 shows patient demographics and screening histories. Median age at first diagnosis was 64 years for both cases and controls and median age at death for cases was 71 years. Whilst the distributions of the number of screening invitations in the two study groups were comparable, differences can be noted in screening attendance, with 72% of the cases versus 82% of the controls attending their first screening invitation; 64% of the cases versus 76% of the controls attending their last screening invitation before diagnosis/pseudodiagnosis; and 21% of the cases versus 12% of the controls never being screened. Median time between last screen and date of diagnosis/pseudodiagnosis for compliers was also slightly longer for cases. From the data available on cervical screening history up to the date of diagnosis/pseudodiagnosis, it can be noted that 22% of the cases compared with 19% of the controls never had a cervical screen.

Table  2 summarises the main results without and with correction for self-selection bias. Using data from cervical screening attendance, the self-selection correction factor was estimated to be 0.78 (95% CI 0.73–0.84). The primary endpoint, the association between attending one or more screens and death from breast cancer, had a resulting OR = 0.49 (95% CI 0.45–0.53) and, when corrected for self-selection, had OR = 0.62 (95% CI 0.56–0.69) by our first method and OR = 0.63 (95% CI 0.55–0.71) by our second. Using the second method, the estimate of the effect of invitation to screening was a 26% reduction in breast cancer mortality (OR = 0.74, 95% CI 0.68-0.81). The unmatched logistic regression on the larger dataset for sensitivity analyses showed a similar effect of screening on breast cancer mortality both before and after controlling for age at diagnosis/pseudodiagnosis and screening area (in both cases, uncorrected OR = 0.55, 95% CI 0.51–0.59).

In order to analyse changes of the effect of screening over time, we excluded women diagnosed before year 2000 (13% of the total records), which led to a corrected OR of 0.56 (95% CI 0.51–0.63) for the effect of ever attending mammographic screening on breast cancer mortality. Women diagnosed from year 2003 onwards had an even larger benefit from being screened (OR corrected by first method = 0.53, 95% CI 0.47–0.59). The estimated effect continued to increase as we restricted the year of diagnosis/pseudodiagnosis further in time (Supplementary Fig.  1 ).

Table  3 shows how the effect of screening varies depending on how much time has passed between a woman’s last screen and her diagnosis/pseudodiagnosis. Screen-detected cancers (assumed to be cancers diagnosed within three months of screening) showed a positive association with breast cancer fatality, after self-selection bias correction by our first method (OR = 1.93, 95% CI 1.68–2.22), while women screened in any other time interval were at reduced risk of dying from breast cancer. This was lowest for women screened in the last year (OR corrected by our first method = 0.19, 95% CI 0.17–0.23) and gradually increased, while still conferring a beneficial effect to screening, for women screened further back in time with respect to their date of diagnosis/pseudodiagnosis. Results using our alternative correction for self-selection were very similar (Table  3 ). Note that the time is from screening to diagnosis, not to death. The Table shows risk of subsequently dying of breast cancer increasing by the time between the screen and diagnosis/pseudodiagnosis.

A similar analysis is shown in Table  4 and Fig.  2 for different time intervals after stratifying for three different age categories at diagnosis/pseudodiagnosis (younger than 60 years, between 60 and 64 years, and 65 years or older). The results show that the protective effect of a screen is greater and lasts longer in the oldest group. The benefit of attending screening in the three years prior to diagnosis/pseudodiagnosis, the recommended interval for screening in the NHS BSP, is shown in the final row of Table  4 , and shows close to a halving of risk with screening within the recommended interval, following self-selection correction by our first method (OR = 0.51, 95% CI 0.46–0.57). Results using our second method of correction were very similar to those using the first (Supplementary Table  1 ). The estimated effect of invitation to screening within the last 36 months using our second method was a 33% reduction in breast cancer mortality (OR = 0.67, 95% CI 0.61–0.73).

Note: the coordinates on the x -axis are the midpoints of the time intervals: 0–3, 3–6, 6–18, 18–36, 36–54 and 54–72 months.

Despite the many improvements in treatments, diagnostic procedures and technologies over the last thirty years, and changes in baseline rate of breast cancer mortality, our data showed an overall reduction in the risk of dying from breast cancer of ~38% for women attending at least one mammography screen, after adjusting for self-selection bias. This is in line with the results obtained from the pilot phase of the study, 10 in which a mortality reduction of 39% was seen for women attending screening in London (deaths occurring in 2008–2009). Using the same calculation method as in the review by the Independent UK Panel on Breast Cancer Screening UK Independent Review, 17 this would correspond to approximately nine breast cancer deaths prevented for every 1,000 women attending screening at ages 50–69 years, larger than but in the same general scale as the six deaths estimated from the UK Independent review.

It should be noted that there is a wide range of estimates of the absolute mortality benefit of mammography screening 18 , 19 , 20 , 21 some finding considerably smaller benefits than above. The size of the estimated effect depends on sources used and assumptions made. However, it has been shown to depend more crucially on whether the effect pertains to screening per se or to invitation to screening only, and on the timescale envisaged. 22 Screening prevents deaths not this year or next, but 5, 10, 15 or 20 years from now. Considering the effect of screening on 10-year mortality will considerably underestimate the absolute benefit. Nevertheless, it should be acknowledged that while the body of evidence, randomised and observational, points to a substantial reduction in breast cancer mortality with screening, there is sufficient variation that different views are still possible.

Our first method of correction for self-selection caused a decrease of about 25% in the estimated protective effect of screening for women having at least one mammogram. The second method yielded similar results. This is a greater correction than the one estimated in the pilot phase, 10 where self-selection only played a minor role, despite the fact that the final risk reduction is very similar. London has a lower coverage than the rest of England for both breast and cervical screening, which is largely explained by factors like deprivation and ethnicity. 23 Such variations in coverage might be one of the causes for the different impact of self-selection between the two phases of the study. For example, a larger population of non-participants, such as in London, may be less different in health status than a smaller population. In the Swedish two-County trial, 24 where only 15% of the population were non-participants, the rate of death from breast cancer in this population was very high. It is also worth noting that, during the early 21st century, breast screening attendance was rapidly increasing in London, and the socioeconomic gradient in attendance was reducing with time nationally. 25 , 26

Case-control studies tend to give higher estimates of benefit than other evaluations, largely because they assess the effect of actually being screened rather than simply being invited to screening. 19 , 27 It should be noted that with our second correction for self-selection bias, we were able to estimate the effect of invitation, giving a 26% breast cancer mortality reduction, similar to the effect observed in the randomised trials in this age group and to the prospectively estimated effect of a 25% reduction in the Copenhagen screening programme. 28 As a comparison, in the review by the Independent UK Panel on Breast Cancer Screening, 17 a meta-analysis of 11 RCTs found that the relative risk reduction of breast cancer mortality for women invited to screening was 20%. Furthermore, in the same report, the panel stated that the case-control studies that they had analysed seemed to inflate the benefit of screening compared to the trials and postulated that this may have been caused by some residual bias unaccounted for by the authors. We believe that our adjustments for self-selection bias has largely accounted for this and that the greater effect of screening in this study is due to technical improvements in mammography since the RCTs were carried out, accompanied by improved treatment and strong quality assurance measures in the NHS BSP. 11

The greater benefit of screening observed for women diagnosed after year 2000 was similar to the pilot study, 10 but here we were able to restrict the analysis to later years of diagnosis and see the benefit getting larger (data not shown). We could conjecture that this improvement was due to the introduction of better procedures in the NHS BSP, such as two-view mammography at every attendance in year 2000 4 ; however, there may be a bias in comparing different times since diagnosis as we only have data on deaths in years 2010–2011. In the first place, cases diagnosed before 2000 have a long survival by definition, and there might therefore be an over-representation of screen-detected cancers. In other words, it is more likely that a case diagnosed before year 2000, for example, who had a breast cancer for more than 10–11 years before dying from it, had a screen-detected cancer rather than a symptomatic one. This confers a bias against screening in the analysis of cancers diagnosed prior to the year 2000. In the second place, there will be a bias in favour of screening if the analysis is restricted to cancers diagnosed within a short time before death, i.e. if we only consider women (pseudo)diagnosed a few years before 2010–2011. We are therefore unable to make any definitive conclusions on the impact of any improvements in the NHS BSP over time.

As shown in RCTs of breast screening, 24 measures of the benefit of screening are largely influenced by the consequent reduction in mortality from symptomatic cancers. This is due to the fact that screen-detected cancers (defined as the ones diagnosed within three months of a screen), despite being less fatal overall, represent a larger proportion of the cancer-related deaths in the immediate period after a screen as it can be seen from the spike in excess mortality in Fig.  2 .

The duration of the benefit of attending screening appears to be greater in older women (Table  4 and Fig.  2 ). Women aged 65 or more see the greatest and longer lasting benefit, which might suggest that they could be screened less often than younger women. This result is in agreement with the impact of ageing on breast cancer biology 29 and is also potentially important in light of the recent incident in the NHS BSP, where a number of women aged 69 and 70 years did not receive the scheduled invitation to their last screening appointment. 30 The exact number affected has been debated but an Independent Review concluded that 5000 women were not invited as scheduled, and that a further 62,000 could be interpreted as having missed their final invitation as defined in the service specification. 30 Our findings suggest that the effect of a delayed screen in older women has a lesser consequence for increased risk of breast cancer mortality than it would have had in younger women. While three years is a longer interval than other programmes in Europe and North America, and further slippage of the interval should be avoided if at all possible, these results could also be used as guidelines for screening units at times of capacity constraints, with the provision that all women receive an opportunity for a final screen around or shortly after age 70. There is interest in stratified screening and these results may inform further thinking on this subject.

A limitation of the study is the retrospective design and the potential for self-selection bias. We have corrected for this in two different ways and for one of these, an effect of invitation to screening was derived which was consistent with trials results and prospective studies for this age group. However, it must be acknowledged that there remains some uncertainty about the extent of self-selection bias. Furthermore, case-control studies for cancer screening programmes are subject to an inherent type of anti-screening bias known as screening opportunity bias. 27 As most of the controls do not have a breast cancer diagnosis, the only way they can be exposed to screening is if they attended a mammography appointment in the past. Cases, on the other hand, may have had a screen in the past, but some of them will also have an additional screen for when their cancer was diagnosed. This induces an artificially higher retrospective probability of screening exposure among cases. Screening opportunity bias was corrected for in the pilot study, 10 where a 10–15% increase in mortality reduction was seen following this, but here we preferred to keep a conservative approach and not adjust for it. To minimise biases with respect to age and opportunity to be screened, we matched very closely for age. This meant that in 1107 cases out of 9550, we could only find one control.

Although the effect of the NHS BSP in preventing breast cancer mortality has been assessed several times, 31 , 32 , 33 , 34 we are aware of only one other case-control study conducted using national data. 34 The latter relies on data up to year 2005 (diagnoses and deaths took place between 1991 and 2005), while ours uses more recent data up to year 2012, arguably more in the epoch of effective adjuvant systemic therapies. It is of interest that our more recent case base shows similar results in terms of the reduction in risk of breast cancer death with screening. In any case, we suggest that it would be of interest to repeat this type of analysis for years thereafter, to ensure that the programme continues to deliver its aims even with the introduction of new diagnostic technologies (e.g. digital mammography). Before the establishment of the NHS BSP in 1987, it was suggested that a routine case-control assessment could and should be part of an ongoing evaluation of a mass screening programme. 35 For this reason, we believe that this exercise should be held on a two-yearly basis.

The results of further national case-control studies (1) evaluating the effect of the NHS BSP on breast cancer incidence and incidence of late stage disease, (2) estimating overdiagnosis, and (3) analysing the interplay of early detection, pathology and treatment on fatality of breast cancer will be published shortly.

To conclude, this study showed that the breast screening programme in England continues to play an important role in the control of breast cancer. The effect of screening within the NHS BSP in England is stronger and longer lasting in women aged 65 or over, but it remains highly relevant for younger women.

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Acknowledgements

Data for this study is based on information collected and quality assured by the PHE National Cancer Registration and Analysis Service. Access to the data was facilitated by the PHE Office for Data Release. We would like to thank Rachael Brannan from the PHE Office for Data Release and David Graham from NHS Digital for their help with the data selection and matching of cases and controls. This work uses data provided by patients and collected by the NHS as part of their care and support.

Author information

These authors contributed equally: Roberta Maroni, Nathalie J Massat

These authors jointly supervised this work: Peter D Sasieni, Stephen W Duffy

Authors and Affiliations

Centre for Cancer Prevention, Wolfson Institute of Preventive Medicine, Queen Mary University of London, Charterhouse Square, London, EC1M 6BQ, UK

Roberta Maroni, Nathalie J. Massat, Dharmishta Parmar, Amanda Dibden, Jack Cuzick & Stephen W. Duffy

Faculty of Life Sciences and Medicine, Cancer Prevention Group, School of Cancer and Pharmaceutical Sciences, King’s College London, Guy’s Campus, Great Maze Pond, London, SE1 9RT, UK

• Peter D. Sasieni

You can also search for this author in PubMed   Google Scholar

Contributions

R.M. oversaw the first draft of the manuscript draft and submission. N.J.M., J.C., P.D.S. and S.W.D. designed the study. D.P. contributed to data collection and cleaning. A.D. assisted with data interpretation. R.M. and S.W.D. analysed the data and produced the figures. All the authors critically reviewed the paper.

Corresponding author

Correspondence to Stephen W. Duffy .

Ethics declarations

Ethics approval and consent to participate.

The study protocol was reviewed and approved by the Department of Health. Ethical approval was obtained from the London Research Ethics Committee of the National Research Ethics Service (reference: 12/LO/1041), and by the National Information Governance Board Ethics and Confidentiality Committee (reference: ECC 6–05 (e)/2012). The ethics committee agreed that informed consent to participate for the study subjects was not necessary. The study was performed in accordance with the Declaration of Helsinki.

Data availability

Data were saved on the servers of the Barts Cancer Institute, Queen Mary University of London, in a folder with restricted access to D.P. A clean, anonymised version of the data was produced and made available to R.M., A.D. and S.W.D. with restricted access to the staff of the Policy Research Unit in Cancer Awareness, Screening and Early Diagnosis at Queen Mary University of London. The data were obtained via the Office for Data Release at Public Health England. We do not have authority to share the data with others, but requests for access to data will be forwarded to the Office for Data Release.

Competing interests

P.D.S. reports personal fees from GRAIL Bio outside the submitted work. J.C. and S.W.D. are members of the editorial board of the British Journal of Cancer. The remaining authors declare no competing interests.

Funding information

his research is funded by the National Institute for Health Research (NIHR) Policy Research Programme, conducted through the Policy Research Unit (PRU) in Cancer Awareness, Screening and Early Diagnosis, PR-PRU-1217-21601. The PRU is a collaboration between researchers from seven institutions (Queen Mary University of London, University College London, King’s College London, London School of Hygiene and Tropical Medicine, Hull York Medical School, Durham University, and Peninsula Medical School). The views expressed are those of the authors and not necessarily those of the NIHR or the Department of Health and Social Care. The funding body was not involved in design, data collection, analysis or interpretation. The funding body had sight of the paper prior to publication but has not had input to its content.

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Maroni, R., Massat, N.J., Parmar, D. et al. A case-control study to evaluate the impact of the breast screening programme on mortality in England. Br J Cancer 124 , 736–743 (2021). https://doi.org/10.1038/s41416-020-01163-2

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Published : 23 November 2020

Issue Date : 16 February 2021

DOI : https://doi.org/10.1038/s41416-020-01163-2

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15. Case-control studies

• Published: April 1997
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Case-control (or case-referent) studies compare patients with a disease or health outcome of interest (a case) with controls who do not have the disease or outcome. Their relevant past exposures are assessed retrospectively, and an estimate of relative risk (odds ratio) determined. This chapter describes the choice of study population, and the key features of selection of cases and determination of their relevant exposures. Selection of controls is a vexed subject, and the chapter considers in detail the associated issues, including matching, loss of controls from the study, and controls who go on to become cases. The chapter concludes with a discussion of study size and statistical power, and the appropriate statistical techniques for estimating and interpreting odds ratio, attributable risk percent, and population attributable risk percent. The problem of interpreting an association as evidence of causation is discussed.

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The case study approach

Sarah crowe.

1 Division of Primary Care, The University of Nottingham, Nottingham, UK

Kathrin Cresswell

2 Centre for Population Health Sciences, The University of Edinburgh, Edinburgh, UK

Ann Robertson

3 School of Health in Social Science, The University of Edinburgh, Edinburgh, UK

Anthony Avery

Aziz sheikh.

The case study approach allows in-depth, multi-faceted explorations of complex issues in their real-life settings. The value of the case study approach is well recognised in the fields of business, law and policy, but somewhat less so in health services research. Based on our experiences of conducting several health-related case studies, we reflect on the different types of case study design, the specific research questions this approach can help answer, the data sources that tend to be used, and the particular advantages and disadvantages of employing this methodological approach. The paper concludes with key pointers to aid those designing and appraising proposals for conducting case study research, and a checklist to help readers assess the quality of case study reports.

Introduction

The case study approach is particularly useful to employ when there is a need to obtain an in-depth appreciation of an issue, event or phenomenon of interest, in its natural real-life context. Our aim in writing this piece is to provide insights into when to consider employing this approach and an overview of key methodological considerations in relation to the design, planning, analysis, interpretation and reporting of case studies.

The illustrative 'grand round', 'case report' and 'case series' have a long tradition in clinical practice and research. Presenting detailed critiques, typically of one or more patients, aims to provide insights into aspects of the clinical case and, in doing so, illustrate broader lessons that may be learnt. In research, the conceptually-related case study approach can be used, for example, to describe in detail a patient's episode of care, explore professional attitudes to and experiences of a new policy initiative or service development or more generally to 'investigate contemporary phenomena within its real-life context' [ 1 ]. Based on our experiences of conducting a range of case studies, we reflect on when to consider using this approach, discuss the key steps involved and illustrate, with examples, some of the practical challenges of attaining an in-depth understanding of a 'case' as an integrated whole. In keeping with previously published work, we acknowledge the importance of theory to underpin the design, selection, conduct and interpretation of case studies[ 2 ]. In so doing, we make passing reference to the different epistemological approaches used in case study research by key theoreticians and methodologists in this field of enquiry.

This paper is structured around the following main questions: What is a case study? What are case studies used for? How are case studies conducted? What are the potential pitfalls and how can these be avoided? We draw in particular on four of our own recently published examples of case studies (see Tables ​ Tables1, 1 , ​ ,2, 2 , ​ ,3 3 and ​ and4) 4 ) and those of others to illustrate our discussion[ 3 - 7 ].

Example of a case study investigating the reasons for differences in recruitment rates of minority ethnic people in asthma research[ 3 ]

Example of a case study investigating the process of planning and implementing a service in Primary Care Organisations[ 4 ]

Example of a case study investigating the introduction of the electronic health records[ 5 ]

Example of a case study investigating the formal and informal ways students learn about patient safety[ 6 ]

What is a case study?

A case study is a research approach that is used to generate an in-depth, multi-faceted understanding of a complex issue in its real-life context. It is an established research design that is used extensively in a wide variety of disciplines, particularly in the social sciences. A case study can be defined in a variety of ways (Table ​ (Table5), 5 ), the central tenet being the need to explore an event or phenomenon in depth and in its natural context. It is for this reason sometimes referred to as a "naturalistic" design; this is in contrast to an "experimental" design (such as a randomised controlled trial) in which the investigator seeks to exert control over and manipulate the variable(s) of interest.

Definitions of a case study

Stake's work has been particularly influential in defining the case study approach to scientific enquiry. He has helpfully characterised three main types of case study: intrinsic , instrumental and collective [ 8 ]. An intrinsic case study is typically undertaken to learn about a unique phenomenon. The researcher should define the uniqueness of the phenomenon, which distinguishes it from all others. In contrast, the instrumental case study uses a particular case (some of which may be better than others) to gain a broader appreciation of an issue or phenomenon. The collective case study involves studying multiple cases simultaneously or sequentially in an attempt to generate a still broader appreciation of a particular issue.

These are however not necessarily mutually exclusive categories. In the first of our examples (Table ​ (Table1), 1 ), we undertook an intrinsic case study to investigate the issue of recruitment of minority ethnic people into the specific context of asthma research studies, but it developed into a instrumental case study through seeking to understand the issue of recruitment of these marginalised populations more generally, generating a number of the findings that are potentially transferable to other disease contexts[ 3 ]. In contrast, the other three examples (see Tables ​ Tables2, 2 , ​ ,3 3 and ​ and4) 4 ) employed collective case study designs to study the introduction of workforce reconfiguration in primary care, the implementation of electronic health records into hospitals, and to understand the ways in which healthcare students learn about patient safety considerations[ 4 - 6 ]. Although our study focusing on the introduction of General Practitioners with Specialist Interests (Table ​ (Table2) 2 ) was explicitly collective in design (four contrasting primary care organisations were studied), is was also instrumental in that this particular professional group was studied as an exemplar of the more general phenomenon of workforce redesign[ 4 ].

What are case studies used for?

According to Yin, case studies can be used to explain, describe or explore events or phenomena in the everyday contexts in which they occur[ 1 ]. These can, for example, help to understand and explain causal links and pathways resulting from a new policy initiative or service development (see Tables ​ Tables2 2 and ​ and3, 3 , for example)[ 1 ]. In contrast to experimental designs, which seek to test a specific hypothesis through deliberately manipulating the environment (like, for example, in a randomised controlled trial giving a new drug to randomly selected individuals and then comparing outcomes with controls),[ 9 ] the case study approach lends itself well to capturing information on more explanatory ' how ', 'what' and ' why ' questions, such as ' how is the intervention being implemented and received on the ground?'. The case study approach can offer additional insights into what gaps exist in its delivery or why one implementation strategy might be chosen over another. This in turn can help develop or refine theory, as shown in our study of the teaching of patient safety in undergraduate curricula (Table ​ (Table4 4 )[ 6 , 10 ]. Key questions to consider when selecting the most appropriate study design are whether it is desirable or indeed possible to undertake a formal experimental investigation in which individuals and/or organisations are allocated to an intervention or control arm? Or whether the wish is to obtain a more naturalistic understanding of an issue? The former is ideally studied using a controlled experimental design, whereas the latter is more appropriately studied using a case study design.

Case studies may be approached in different ways depending on the epistemological standpoint of the researcher, that is, whether they take a critical (questioning one's own and others' assumptions), interpretivist (trying to understand individual and shared social meanings) or positivist approach (orientating towards the criteria of natural sciences, such as focusing on generalisability considerations) (Table ​ (Table6). 6 ). Whilst such a schema can be conceptually helpful, it may be appropriate to draw on more than one approach in any case study, particularly in the context of conducting health services research. Doolin has, for example, noted that in the context of undertaking interpretative case studies, researchers can usefully draw on a critical, reflective perspective which seeks to take into account the wider social and political environment that has shaped the case[ 11 ].

Example of epistemological approaches that may be used in case study research

How are case studies conducted?

Here, we focus on the main stages of research activity when planning and undertaking a case study; the crucial stages are: defining the case; selecting the case(s); collecting and analysing the data; interpreting data; and reporting the findings.

Defining the case

Carefully formulated research question(s), informed by the existing literature and a prior appreciation of the theoretical issues and setting(s), are all important in appropriately and succinctly defining the case[ 8 , 12 ]. Crucially, each case should have a pre-defined boundary which clarifies the nature and time period covered by the case study (i.e. its scope, beginning and end), the relevant social group, organisation or geographical area of interest to the investigator, the types of evidence to be collected, and the priorities for data collection and analysis (see Table ​ Table7 7 )[ 1 ]. A theory driven approach to defining the case may help generate knowledge that is potentially transferable to a range of clinical contexts and behaviours; using theory is also likely to result in a more informed appreciation of, for example, how and why interventions have succeeded or failed[ 13 ].

Example of a checklist for rating a case study proposal[ 8 ]

For example, in our evaluation of the introduction of electronic health records in English hospitals (Table ​ (Table3), 3 ), we defined our cases as the NHS Trusts that were receiving the new technology[ 5 ]. Our focus was on how the technology was being implemented. However, if the primary research interest had been on the social and organisational dimensions of implementation, we might have defined our case differently as a grouping of healthcare professionals (e.g. doctors and/or nurses). The precise beginning and end of the case may however prove difficult to define. Pursuing this same example, when does the process of implementation and adoption of an electronic health record system really begin or end? Such judgements will inevitably be influenced by a range of factors, including the research question, theory of interest, the scope and richness of the gathered data and the resources available to the research team.

Selecting the case(s)

The decision on how to select the case(s) to study is a very important one that merits some reflection. In an intrinsic case study, the case is selected on its own merits[ 8 ]. The case is selected not because it is representative of other cases, but because of its uniqueness, which is of genuine interest to the researchers. This was, for example, the case in our study of the recruitment of minority ethnic participants into asthma research (Table ​ (Table1) 1 ) as our earlier work had demonstrated the marginalisation of minority ethnic people with asthma, despite evidence of disproportionate asthma morbidity[ 14 , 15 ]. In another example of an intrinsic case study, Hellstrom et al.[ 16 ] studied an elderly married couple living with dementia to explore how dementia had impacted on their understanding of home, their everyday life and their relationships.

For an instrumental case study, selecting a "typical" case can work well[ 8 ]. In contrast to the intrinsic case study, the particular case which is chosen is of less importance than selecting a case that allows the researcher to investigate an issue or phenomenon. For example, in order to gain an understanding of doctors' responses to health policy initiatives, Som undertook an instrumental case study interviewing clinicians who had a range of responsibilities for clinical governance in one NHS acute hospital trust[ 17 ]. Sampling a "deviant" or "atypical" case may however prove even more informative, potentially enabling the researcher to identify causal processes, generate hypotheses and develop theory.

In collective or multiple case studies, a number of cases are carefully selected. This offers the advantage of allowing comparisons to be made across several cases and/or replication. Choosing a "typical" case may enable the findings to be generalised to theory (i.e. analytical generalisation) or to test theory by replicating the findings in a second or even a third case (i.e. replication logic)[ 1 ]. Yin suggests two or three literal replications (i.e. predicting similar results) if the theory is straightforward and five or more if the theory is more subtle. However, critics might argue that selecting 'cases' in this way is insufficiently reflexive and ill-suited to the complexities of contemporary healthcare organisations.

The selected case study site(s) should allow the research team access to the group of individuals, the organisation, the processes or whatever else constitutes the chosen unit of analysis for the study. Access is therefore a central consideration; the researcher needs to come to know the case study site(s) well and to work cooperatively with them. Selected cases need to be not only interesting but also hospitable to the inquiry [ 8 ] if they are to be informative and answer the research question(s). Case study sites may also be pre-selected for the researcher, with decisions being influenced by key stakeholders. For example, our selection of case study sites in the evaluation of the implementation and adoption of electronic health record systems (see Table ​ Table3) 3 ) was heavily influenced by NHS Connecting for Health, the government agency that was responsible for overseeing the National Programme for Information Technology (NPfIT)[ 5 ]. This prominent stakeholder had already selected the NHS sites (through a competitive bidding process) to be early adopters of the electronic health record systems and had negotiated contracts that detailed the deployment timelines.

It is also important to consider in advance the likely burden and risks associated with participation for those who (or the site(s) which) comprise the case study. Of particular importance is the obligation for the researcher to think through the ethical implications of the study (e.g. the risk of inadvertently breaching anonymity or confidentiality) and to ensure that potential participants/participating sites are provided with sufficient information to make an informed choice about joining the study. The outcome of providing this information might be that the emotive burden associated with participation, or the organisational disruption associated with supporting the fieldwork, is considered so high that the individuals or sites decide against participation.

In our example of evaluating implementations of electronic health record systems, given the restricted number of early adopter sites available to us, we sought purposively to select a diverse range of implementation cases among those that were available[ 5 ]. We chose a mixture of teaching, non-teaching and Foundation Trust hospitals, and examples of each of the three electronic health record systems procured centrally by the NPfIT. At one recruited site, it quickly became apparent that access was problematic because of competing demands on that organisation. Recognising the importance of full access and co-operative working for generating rich data, the research team decided not to pursue work at that site and instead to focus on other recruited sites.

Collecting the data

In order to develop a thorough understanding of the case, the case study approach usually involves the collection of multiple sources of evidence, using a range of quantitative (e.g. questionnaires, audits and analysis of routinely collected healthcare data) and more commonly qualitative techniques (e.g. interviews, focus groups and observations). The use of multiple sources of data (data triangulation) has been advocated as a way of increasing the internal validity of a study (i.e. the extent to which the method is appropriate to answer the research question)[ 8 , 18 - 21 ]. An underlying assumption is that data collected in different ways should lead to similar conclusions, and approaching the same issue from different angles can help develop a holistic picture of the phenomenon (Table ​ (Table2 2 )[ 4 ].

Brazier and colleagues used a mixed-methods case study approach to investigate the impact of a cancer care programme[ 22 ]. Here, quantitative measures were collected with questionnaires before, and five months after, the start of the intervention which did not yield any statistically significant results. Qualitative interviews with patients however helped provide an insight into potentially beneficial process-related aspects of the programme, such as greater, perceived patient involvement in care. The authors reported how this case study approach provided a number of contextual factors likely to influence the effectiveness of the intervention and which were not likely to have been obtained from quantitative methods alone.

In collective or multiple case studies, data collection needs to be flexible enough to allow a detailed description of each individual case to be developed (e.g. the nature of different cancer care programmes), before considering the emerging similarities and differences in cross-case comparisons (e.g. to explore why one programme is more effective than another). It is important that data sources from different cases are, where possible, broadly comparable for this purpose even though they may vary in nature and depth.

Analysing, interpreting and reporting case studies

Making sense and offering a coherent interpretation of the typically disparate sources of data (whether qualitative alone or together with quantitative) is far from straightforward. Repeated reviewing and sorting of the voluminous and detail-rich data are integral to the process of analysis. In collective case studies, it is helpful to analyse data relating to the individual component cases first, before making comparisons across cases. Attention needs to be paid to variations within each case and, where relevant, the relationship between different causes, effects and outcomes[ 23 ]. Data will need to be organised and coded to allow the key issues, both derived from the literature and emerging from the dataset, to be easily retrieved at a later stage. An initial coding frame can help capture these issues and can be applied systematically to the whole dataset with the aid of a qualitative data analysis software package.

The Framework approach is a practical approach, comprising of five stages (familiarisation; identifying a thematic framework; indexing; charting; mapping and interpretation) , to managing and analysing large datasets particularly if time is limited, as was the case in our study of recruitment of South Asians into asthma research (Table ​ (Table1 1 )[ 3 , 24 ]. Theoretical frameworks may also play an important role in integrating different sources of data and examining emerging themes. For example, we drew on a socio-technical framework to help explain the connections between different elements - technology; people; and the organisational settings within which they worked - in our study of the introduction of electronic health record systems (Table ​ (Table3 3 )[ 5 ]. Our study of patient safety in undergraduate curricula drew on an evaluation-based approach to design and analysis, which emphasised the importance of the academic, organisational and practice contexts through which students learn (Table ​ (Table4 4 )[ 6 ].

Case study findings can have implications both for theory development and theory testing. They may establish, strengthen or weaken historical explanations of a case and, in certain circumstances, allow theoretical (as opposed to statistical) generalisation beyond the particular cases studied[ 12 ]. These theoretical lenses should not, however, constitute a strait-jacket and the cases should not be "forced to fit" the particular theoretical framework that is being employed.

When reporting findings, it is important to provide the reader with enough contextual information to understand the processes that were followed and how the conclusions were reached. In a collective case study, researchers may choose to present the findings from individual cases separately before amalgamating across cases. Care must be taken to ensure the anonymity of both case sites and individual participants (if agreed in advance) by allocating appropriate codes or withholding descriptors. In the example given in Table ​ Table3, 3 , we decided against providing detailed information on the NHS sites and individual participants in order to avoid the risk of inadvertent disclosure of identities[ 5 , 25 ].

What are the potential pitfalls and how can these be avoided?

The case study approach is, as with all research, not without its limitations. When investigating the formal and informal ways undergraduate students learn about patient safety (Table ​ (Table4), 4 ), for example, we rapidly accumulated a large quantity of data. The volume of data, together with the time restrictions in place, impacted on the depth of analysis that was possible within the available resources. This highlights a more general point of the importance of avoiding the temptation to collect as much data as possible; adequate time also needs to be set aside for data analysis and interpretation of what are often highly complex datasets.

Case study research has sometimes been criticised for lacking scientific rigour and providing little basis for generalisation (i.e. producing findings that may be transferable to other settings)[ 1 ]. There are several ways to address these concerns, including: the use of theoretical sampling (i.e. drawing on a particular conceptual framework); respondent validation (i.e. participants checking emerging findings and the researcher's interpretation, and providing an opinion as to whether they feel these are accurate); and transparency throughout the research process (see Table ​ Table8 8 )[ 8 , 18 - 21 , 23 , 26 ]. Transparency can be achieved by describing in detail the steps involved in case selection, data collection, the reasons for the particular methods chosen, and the researcher's background and level of involvement (i.e. being explicit about how the researcher has influenced data collection and interpretation). Seeking potential, alternative explanations, and being explicit about how interpretations and conclusions were reached, help readers to judge the trustworthiness of the case study report. Stake provides a critique checklist for a case study report (Table ​ (Table9 9 )[ 8 ].

Potential pitfalls and mitigating actions when undertaking case study research

Stake's checklist for assessing the quality of a case study report[ 8 ]

Conclusions

The case study approach allows, amongst other things, critical events, interventions, policy developments and programme-based service reforms to be studied in detail in a real-life context. It should therefore be considered when an experimental design is either inappropriate to answer the research questions posed or impossible to undertake. Considering the frequency with which implementations of innovations are now taking place in healthcare settings and how well the case study approach lends itself to in-depth, complex health service research, we believe this approach should be more widely considered by researchers. Though inherently challenging, the research case study can, if carefully conceptualised and thoughtfully undertaken and reported, yield powerful insights into many important aspects of health and healthcare delivery.

Competing interests

The authors declare that they have no competing interests.

Authors' contributions

AS conceived this article. SC, KC and AR wrote this paper with GH, AA and AS all commenting on various drafts. SC and AS are guarantors.

Pre-publication history

The pre-publication history for this paper can be accessed here:

http://www.biomedcentral.com/1471-2288/11/100/prepub

Acknowledgements

We are grateful to the participants and colleagues who contributed to the individual case studies that we have drawn on. This work received no direct funding, but it has been informed by projects funded by Asthma UK, the NHS Service Delivery Organisation, NHS Connecting for Health Evaluation Programme, and Patient Safety Research Portfolio. We would also like to thank the expert reviewers for their insightful and constructive feedback. Our thanks are also due to Dr. Allison Worth who commented on an earlier draft of this manuscript.

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[Case-control studies with multinomial responses: a proposal for analysis]

Affiliation.

• 1 Universidade Estadual de Campinas, Campinas, Brasil. [email protected]
• PMID: 20464064
• DOI: 10.1590/s0102-311x2010000300003

This study reviews articles on case-control studies in which the cases were classified in two or more types. Application of multinomial models and their adequacy for case-control studies are discussed. Among the available multinomial adjustments, we argue that the polytomous logistic model is the most suitable for obtaining epidemiological measures of risk and association in case-control studies. By way of illustration, we present an application of this model in a population-based case-control study, comparing the results with those obtained in a binomial logistic model. The multinomial approach allows investigating, in a single analysis, the occurrence of associations between covariates and more or more subclasses of cases, thus providing the epidemiologically relevant possibility of identifying individualized risk and protective factors for each subclass.

Publication types

• English Abstract
• Research Support, Non-U.S. Gov't
• Case-Control Studies*
• Logistic Models*