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Bias in full cohort and nested case-control studies?

In this issue, Langholz and Richardson 1 and Hein et al. 2 address two recent articles by Deubner and colleagues 3 , 4 about nested case-control studies. In one article, 3 Deubner and colleagues called into question the fundamental validity of the nested case-control design. If their critique is compelling, it would raise doubts about the interpretation of hundreds of publications that report results from nested case-control studies. In another article, 4 the same authors suggested a restriction on control selection in nested case-control studies to make cases and controls more comparable.

Fundamentally, a properly executed case-control study nested in a cohort is valid if the corresponding analysis of the full cohort is valid. The mathematics of the likelihoods are the same for both, 5 as Langholz and Richardson 1 point out, and the same software procedures work for both. The only salient difference between the two designs is whether independent random samples or 100% samples are used in the conditional likelihood factor for each case. As Deubner and his colleagues 3 note, the design and analysis of nested case-control studies are complex, but no more so than the analysis of cohorts, which must consider issues including time scales, various measures of time-dependent variables, and possible censoring.

Generally, the only disadvantages to nested case-control studies are the reduced precision and power due to sampling of controls, and the possibility of flaws in the sampling design or its implementation. Therefore, any problem with nested case-control studies must also be a problem for full cohort analysis. Demonstration of this (or an explanation for this discordance) would add to the credibility of a challenge to the validity of standard analytic methods for nested case-control studies.

Deubner and colleagues provide simulations 3 to show bias in nested case-control studies with a lagged measure of exposure. Each step in their simulation seems reasonable. The authors started with an assembled cohort, for whom age and calendar time of starting and stopping work was available for all cohort members. In each simulation, the authors randomly assigned 142 of the cohort members to be cases, and took the end of their follow-up as the event or endpoint time. Controls matched to each case were selected from at-risk cohort members at the age of the case’s event. A case’s cumulative exposure was measured from time of entry into the cohort until event time. A control’s cumulative exposure was measured from time of entry until the control reached the age at event of the index case to which the control was matched. Analysis was conducted by applied conditional logistic regression.

In fact, a subtle flaw in the design of these simulation studies makes them misleading. As Langholz and Richardson 1 point out, Deubner and colleagues mistakenly chose cases as a random sample of all cohort members; in fact, as in Table 1 of this paper by Hein et al. 2 , the average age-at-event in cases is less than the average age-at-end-of-followup in comparable cohort members, when censoring is not informative and the exposure has no effect on risk of the event or censoring. Why are cases younger at the event? It is because the cases’ age at end of follow-up has to be the minimum of i) the age of death from lung cancer, ii) the age of death from other causes, or iii) the age at other causes of censoring—whereas controls are followed to the minimum of ii) or iii) only. The members of the cohort who did not die from lung cancer will be older than the cases at end of follow-up.

Further, controls’ follow-up time in the simulations tends to begin at an older age than cases’. This is because, to be chosen, controls must be followed at the age of the event in the case, and (as is standard) follow-up time is truncated when the control reaches the age of the index case. Therefore, follow-up time in controls in the simulation will on average be less than follow-up time in the cases, randomly chosen from the cohort and with untruncated follow-up times. Similarly, all measures of exposure that depend on follow-up time (such as duration, average, and cumulative exposure) are distorted even when everyone receives the same level of exposure during follow-up. This phenomenon can be seen in the second row (and possibly the first row) of Table 2 of the paper by Deubner and colleagues 3 where, in the absence of an exposure effect, the cumulative exposure of cases (proportional to follow-up time when exposure is constant) is greater than that of controls. In contrast, the results of the simulations (based on generating the cohort, rather than sampling from an existing cohort) show that cumulative exposure is equal between cases and controls when differences in a time-fixed level of exposure is constant (Table 1, rows 1 and 2).

So why does proportional hazards analysis truncate exposures for controls but not for cases? In proportional hazards analysis of full cohorts and nested case-control studies, the key calculation is the set of conditional probabilities that each case is the one who developed disease among all those in the cohort (or among the case and matched controls in the nested case-control study) under follow-up at case’s age at event, given everyone’s exposure through that age. Logically, any exposure in the case after the event cannot be related to risk at the time of event. Similarly, the other cohort members’ exposures subsequent to the index case’s age at event also should not be allowed to affect the conditional probability of the event.

I do not agree with Deubner and colleagues that lagging raises special concerns. A lagged measure of exposure with lag L bases risk at a given time point t only on exposure through time point t – L . Lagging is simply one way to measure exposure, and does not differ fundamentally from choosing other metrics such as average exposure, peak exposure, or cumulative exposure without lagging. 1 As long as exposure is measured only up to the time of the event, the particular choice of exposure summary cannot introduce bias in comparing cases and controls. 1

In their second paper, Deubner and colleagues (this time with Levy as the first author 4 ) suggest the use of risk-set members’ age at the end of follow-up as a control selection criterion. Specifically, they advocate choosing only controls whose age at end of follow-up is close to the index case’s age at death, in order to avoid imbalance between cases and controls in age at start of followup or of first exposure and in age at censoring. Unfortunately, the use of risk set members’ age at end of follow-up as a control selection criterion generates nonrandom samples. As Lubin and Gail 6 state (and Levy et al 4 quote),it is essential to choose a random sample from the risk set. Indeed, Hein et al., 2 (Table 1, row 3) show that there is a bias generated from a non-random sample with controls who are younger at end of follow-up than the average in the risk set. The extra restriction proposed by Levy et al. 4 can also cause another bias: if a time-independent exposure, one whose value is constant during follow-up, causes censoring due to death from another cause, the average exposure of cohort members in the risk set with follow-up even only slightly beyond the time of diagnosis of the case will tend to be less than the average in the risk set. Thus, the difference in exposure between cases and controls – and its estimated effect – will be exaggerated, even under the usual assumption of independent censoring. By contrast, the full cohort analysis will not have an analogous restriction and will be valid under independent censoring.

In my view, the two papers published in this issue 1 , 2 and the arguments offered here provide a persuasive defense of the standard analytic approach for nested case control designs. Although perhaps compelling at first look, the arguments by Deubner and his colleagues 3 , 4 about lagged exposure do not in fact undermine the standard analysis. The setup of their simulation contains an error, and their results are not confirmed by others. These authors offer no explanation of why the bias with lagged exposures would be restricted to nested case-control studies and not be present in the full cohort analysis. Their suggestion of nonrandom selection of controls could itself induce bias. Taking all things into account, their critique is not a valid criticism of this familiar and useful epidemiologic approach. Even so, such challenges to the status quo as offered by Deubner and colleagues are not without benefit – they push us to a better understanding of the fundamental principles that underlie our methods.


This research was supported in part by the Intramural Research Program of the NIH, National Cancer Institute, Division of Cancer Epidemiology and Genetics.

The author thanks Dr. Kyle Steenland, Emory University, for help in preparation of this manuscript.

  • Research article
  • Open access
  • Published: 14 May 2020

Application of the matched nested case-control design to the secondary analysis of trial data

  • Christopher Partlett   ORCID: orcid.org/0000-0001-5139-3412 1 , 2 ,
  • Nigel J. Hall 3 ,
  • Alison Leaf 4 , 2 ,
  • Edmund Juszczak 2 &
  • Louise Linsell 2  

BMC Medical Research Methodology volume  20 , Article number:  117 ( 2020 ) Cite this article

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A nested case-control study is an efficient design that can be embedded within an existing cohort study or randomised trial. It has a number of advantages compared to the conventional case-control design, and has the potential to answer important research questions using untapped prospectively collected data.

We demonstrate the utility of the matched nested case-control design by applying it to a secondary analysis of the Abnormal Doppler Enteral Prescription Trial. We investigated the role of milk feed type and changes in milk feed type in the development of necrotising enterocolitis in a group of 398 high risk growth-restricted preterm infants.

Using matching, we were able to generate a comparable sample of controls selected from the same population as the cases. In contrast to the standard case-control design, exposure status was ascertained prior to the outcome event occurring and the comparison between the cases and matched controls could be made at the point at which the event occurred. This enabled us to reliably investigate the temporal relationship between feed type and necrotising enterocolitis.


A matched nested case-control study can be used to identify credible associations in a secondary analysis of clinical trial data where the exposure of interest was not randomised, and has several advantages over a standard case-control design. This method offers the potential to make reliable inferences in scenarios where it would be unethical or impractical to perform a randomised clinical trial.

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Key messages

A matched nested case-control design provides an efficient way to investigate causal relationships using untapped data from prospective cohort studies and randomised controlled trials

This method has several advantages over a standard case-control design, particularly when studying time-dependent exposures on rare outcomes

It offers the potential to make reliable inferences in scenarios where unethical or practical issues preclude the use of a randomised controlled trial

Randomised controlled trials (RCTs) are regarded as the gold standard in evidence based medicine, due to their prospective design and the minimisation of important sources of bias through the use of randomisation, allocation concealment and blinding. However, RCTs are not always appropriate due to ethical or practical issues, particularly when investigating risk factors for an outcome. If beliefs about the causal role of a risk factor are already embedded within a clinical community, based on concrete evidence or otherwise, then it is not possible to conduct an RCT due to lack of equipoise. It is often not feasible to randomise potential risk factors, for example, if they are biological or genetic or if there is a strong element of patient preference involved. In such scenarios, the main alternative is to conduct an observational study; either a prospective cohort study which can be complicated and costly, or a retrospective case-control study with methodological shortcomings.

The nested case-control study design employs case-control methodology within an established prospective cohort study [ 1 ]. It first emerged in the 1970–80s and was typically used when it was expensive or difficult to obtain data on a particular exposure for all members of the cohort; instead a subset of controls would be selected at random [ 2 ]. This method with the use of matching has been shown to be an efficient design that can be used to provide unbiased estimates of relative risk with considerable cost savings [ 3 , 4 , 5 ]. Cases who develop the outcome of interest at a given point in time are matched to a random subset of members of the cohort who have not experienced the outcome at that time. These controls may develop the outcome later and become a case themselves, and they may also act as a control for other cases [ 6 , 7 ]. This approach has a number of advantages compared to the standard case-control design: (1) cases and controls are sampled from the same population, (2) exposures are measured prior to the outcome occurring, and (3) cases can be matched to controls at the time (e.g. age) of the outcome event.

More recently, the nested case-control design has been used within RCTs to investigate the causative role of risk factors in the development of trial outcomes [ 8 , 9 , 10 ]. In this paper we investigate the utility of the matched nested case-control design in a secondary analysis of the ADEPT: Abnormal Doppler Enteral Prescription Trial (ISRCTN87351483) data, to investigate the role of different types of milk feed (and changes in types of milk feed) in the development of necrotising enterocolitis. We illustrate the use of this methodology and explore issues relating to its implementation. We also discuss and appraise the value of this methodology in answering similar challenging research questions using clinical trial data more generally.

ADEPT: Abnormal Doppler Enteral Prescription Trial (ISRCTN87351483) was funded by Action Medical Research (SP4006) and investigated whether early (24–48 h after birth) or late (120–144 h after birth) introduction of milk feeds was a risk factor for necrotising enterocolitis (NEC) in a population of 404 infants born preterm and growth-restricted, following abnormal antenatal Doppler blood flow velocities [ 11 ]. Consent and randomisation occurred in the first 2 days after birth. There was no difference found in the incidence of NEC between the two groups, however there was interest in the association between feed type (formula/fortifier or exclusive mother/donor breast milk) and the development of NEC. Breast milk is one of few factors believed to reduce the risk of NEC that has been widely adopted into clinical practice, despite a paucity of high quality population based data [ 12 , 13 ]. However, due to lack of equipoise it would not be ethical or feasible to conduct a trial randomising newborn infants to formula or breast milk.

With additional funding from Action Medical Research (GN2506), the authors used a matched nested case-control design to investigate the association between feed type and the development of severe NEC, defined as Bell’s staging Stage II or III [ 14 ], using detailed daily feed log data from the ADEPT trial. The feed type and quantity of feed was recorded daily until an infant had reached full feeds and had ceased parenteral nutrition, or until 28 days after birth, whichever was longest. Using this information, infants were classified according to the following predefined exposures:

Exposure to formula milk or fortifier in the first 14 days of life

Exposure to formula milk or fortifier in the first 28 days of life

Any prior exposure to formula milk or fortifier

Change in feed type (between formula, fortifier or breast milk) within the previous 7 days.

In the remainder of the methods section we discuss the challenges of conducting this analysis and practical issues encountered in applying the matched nested case-control methodology. In the results section we present data from different aspects of the analysis, to illustrate the utility of this approach in answering the research question.

Cohort time axis

For the main trial analysis, time of randomisation was defined as time zero, which is the conventional approach given that events occurring prior to randomisation cannot be influenced by the intervention under investigation. However, for the nested case-control analysis, time zero was defined as day of delivery because age in days was considered easier to interpret, and also it was possible for an outcome event to occur prior to randomisation. Infants were followed up until their exit time, which was defined by the first occurrence of NEC, death or the last daily feed log record.

Case definition

An infant was defined as a case at their first recorded incidence of severe NEC, defined as Bell’s staging Stage II or III [ 14 ]. Infants could only be included as a case once; subsequent episodes of NEC in the same infant were not counted. Once an infant had been identified as a case, they could not be included in any future risk sets for other cases, even if the NEC episode had been resolved.

Risk set definition

One of the major challenges was identifying an appropriate risk set from which controls could be sampled, whilst also allowing the analysis to incorporate the time dependent feed log data and adjust for known confounders. A diagnosis of NEC has a crucial impact on the subsequent feeding of an infant, therefore it was essential that the analysis only included exposure to non-breast milk feeds prior to the onset of NEC. A standard case-control analysis would have produced misleading results in this context, as infants would have been defined as a cases if they had experienced NEC prior to the end of the study period, regardless of the timing of the event in relation to exposure to non-breast milk. Using a matched nested case-control design allowed us to match an infant with a diagnosis of NEC (case) at a given point in time (days from delivery) to infants with similar characteristics (with respect to other important confounding factors), who had not experienced NEC at the failure time of the case. Figure  1 is a schematic diagram of this process. Each time an outcome event occurred (case), infants that were still at risk were eligible to be selected as a control (risk set). A matching algorithm was used to select a sample of controls with similar characteristics from this risk set. Infants selected as controls could go on to become a case themselves, and could also be included in the risk sets for other cases.

figure 1

Schematic diagram illustrating the selection of controls from each risk set. Three days following delivery, an infant develops NEC. At this point, there are 11 infants left in the risk set. Four controls with the closest matching are selected, including one infant that becomes a future case on day 18

Selection of matching factors

An important consideration was the appropriate selection of matching factors as well as identifying the optimum mechanism for matching. Sex, gestational age and birth weight were considered to be clear candidates for matching factors, as they are all associated with the development NEC. Gestational age and birth weight in particular are both likely to impact the infant’s feeding and thus their exposure to non-breast milk feeds. Both gestational age and birth weight were matched simultaneously, because of the strong collinearity between gestational age and birth weight, illustrated in Fig.  2 . This was achieved by minimising the Mahalanobis distance from the case to prospective controls of the same sex [ 15 ]. That is, selecting the control closest in gestational age and birth weight to the case while taking into account the correlation between these characteristics.

figure 2

Scatterplot of birth weight versus gestational age for infants with NEC (cases) and those without (controls)

Typically, treatment allocation would be incorporated as a matching factor since in a secondary analysis it is a nuisance factor imposed by the trial design, which should be accounted for. However, in this example, the ADEPT allocation is associated with likelihood of exposure, since it directly influences the feeding regime. For example, an infant randomised to receive early introduction of feeds is more likely to be exposed to non-breast milk feeds in the first 14 days (44%) than an infant randomised to late introduction of feeds (23%). The main trial results also demonstrated no evidence of association with the outcome (NEC) and therefore there was a concern about the potential for overmatching. Overmatching is caused by inappropriate selection of matching factors (i.e. factors which are not associated with the outcome of interest), which may harm the statistical efficiency of the analysis [ 16 ]. Therefore, we did not include the ADEPT allocation as a matching factor, but we conduct an unadjusted and adjusted analysis by trial arm, to examine its impact on the results.

Selection of controls

Another important consideration was the method used to randomly select controls from each risk set for each case. This can be performed with or without replacement and including or excluding the case in the risk set. We chose the recommended option of sampling without replacement and excluding the case from the risk set, which produces the optimal unbiased estimate of relative risk, with greater statistical efficiency [ 17 , 18 ]. However, infants could be included in multiple risk sets and be selected more than once as a control. We also included future cases of NEC as controls in earlier risk sets, as their exclusion can also lead to biased estimates of relative risk [ 19 ].

Number of controls

In standard case-control studies it has been shown that there is little statistical efficiency gained from having more than four matched controls relative to each case [ 20 , 21 ]. Using five controls is only 4% more efficient than using four, therefore there is no added benefit in using additional controls if a cost is attached, for example taking extra biological samples in a prospective cohort setting. However gains in statistical efficiency are possible by using more than four controls if the probability of exposure among controls is low (< 0.1) [ 4 , 5 ]. Neither of these were issues for this particular analysis, as there were no additional costs involved in using more controls and prevalence of the defined exposures to non-breast milk was over 20% among infants without a diagnosis of NEC. However, there was a concern that including additional controls with increasing distance from the gestational age and birth weight of the case may undermine the matching algorithm. Also, increasing the number of controls sampled per case would lead to an increase in repeated sampling, resulting in larger number of duplicates present in the overall matched control population. This was a particular concern as control duplication was most likely to occur for infants with the lowest birth weight and gestational ages, from which there is a much smaller pool of control infants to sample from. This would have resulted in a small number of infants (with low birth weight and gestational age) being sampled multiple times and having disproportionate weighting in the matched control sample. Therefore, we limited the number of matched controls to four per case.

Statistical analysis

The baseline characteristics of infants with NEC, the matched control group, and all infants with no diagnosis of NEC (non-cases) were compared. Numbers (with percentages) were presented for binary and categorical variables, and means (and standard deviations) or medians (with interquartile range and/or range) for continuous variables. Cases were matched to four controls with the same sex and smallest Mahalanobis distance based on gestational age and birth weight. Conditional logistic regression was used to calculate the odds ratio of developing NEC for cases compared matched controls for each predefined exposure with 95% confidence intervals. Unadjusted odds ratios were calculated, along with estimates adjusting for ADEPT allocation.

The results of the full analysis, including the application of this method to explore the relationship between feed type and other clinically relevant outcomes, are reported in a separate clinical paper (in preparation). Of the 404 infants randomised to ADEPT, 398 were included in this analysis (1 infant was randomised in error, 1 set of parents withdrew consent, 3 infants had no daily feed log data and for 1 infant the severity of NEC was unknown). There were 35 cases of severe NEC and 363 infants without a diagnosis of severe NEC (non-cases). Of the 140 matched controls randomly sampled from the risk set, 109 were unique, 31 were sampled more than once, and 8 had a subsequent diagnosis of severe NEC.

The baseline characteristics of infants with severe NEC (cases) and their matched controls are shown in Table  1 , alongside the characteristics of infants without a diagnosis of severe NEC (non-cases). The matching algorithm successfully produced a well matched collection of controls, based on the majority of these characteristics. There were, however, a slightly higher proportion of infants with the lowest birthweights (< 750 g) among the cases compared to the matched controls (49% vs 38%). The only other factors to show a noticeable difference between cases and matched controls are maternal hypertension (37% vs 49%) and ventilation at trial entry (6% vs 21%), neither of which have been previously identified as risk factors for NEC. Figure  3 shows scatter plots of birth weight and gestational age for the 35 individual cases of NEC and their matched controls, which provides a visual representation of the matching.

figure 3

Scatterplots showing the matched cases and controls for each case of severe NEC. Each panel contains a separate case of NEC and the matched controls

The main results of the adjusted analysis are presented in Fig.  4 . Unadjusted analyses are included in Table A 1 in the supplementary material, alongside a post-hoc sensitivity analysis that additionally includes covariate adjustment for gestational age and birthweight. While the study did not identify any significant trends between feed-type and severe NEC the findings were consistent with the a priori hypothesis, that exposure to non-breast milk feeds is associated with an increased risk of NEC. In addition, the study identified some potential trends in the association of feed-type with other important outcomes, worthy of further investigation.

figure 4

Forest plot showing the adjusted odds ratio comparing severe NEC to exposures. Odds ratios are adjusted for sex, gestational age and birthweight (via matching) and trial arm (via covariate adjustment). a Odds ratio and 95% confidence interval. b 109 unique controls

Employing a matched nested case-control design for this secondary analysis of clinical trial data overcame many of the limitations of a standard case-control analysis. We were able to select controls from the same population as the cases thus avoiding selection bias. Using matching, we were able to create a comparable sample of controls with respect to important clinical characteristics and confounding factors. This method allowed us to reliably investigate the temporal relationship between feed type and severe NEC since the exposure data was collected prospectively prior to the outcome occurring. We were also able to successfully investigate the relationship between feed type and several other important outcomes such as sepsis. A standard case-control analysis is typically based on recall or retrospective data collection once the outcome is known, which can introduce recall bias. If we had performed a simple comparison between cases and non-cases of NEC without taking into account the timing of the exposure, this would have produced misleading results. Another advantage of the matched nested case-control design was that we were able to match cases to controls at the time of the outcome event so that they were of comparable ages. The methodology is especially powerful when the timing of the exposure is of importance, particularly for time-dependent exposures such as the one studied here.

While the efficient use of existing trial data has a number of benefits, there are of course disadvantages to using data that were collected for another primary purpose. For instance, it is possible that such data are less robustly collected and checked. As a result, researchers may be more likely to encounter participants with either invalid or missing data.

For instance, the some of the additional feed log data collected in ADEPT were never intended to be used to answer clinical research questions, rather, their purpose was to monitor the adherence of participants to the intervention or provide added background information. In this study, it was necessary to make assumptions about missing data to fill small gaps in the daily feed logs. Researchers should take care that such assumptions are fully documented in the statistical analysis plan in advance and determined blinded to the outcome. Another option is to plan these sub-studies at the design phase, however, there needs to be a balance between the potential burden of additional data collection and having a streamlined trial that is able to answer the primary research question.

Another limitation of the methodology is that it is only possible to match on known confounders. This is in contrast to a randomised controlled trial, in which it is possible to balance on unknown and unmeasured baseline characteristics. As a consequence, particular care must be given to select important matching factors, but also to avoid overmatching.

The methodology allows for participants to be selected as controls multiple times, so there is the possibility that systematic duplication of a specific subset of participants (e.g. infants with a lower birthweight and smaller gestational age) could lead to a small number of participants disproportionately influencing the results. Within this study, we conducted sensitivity analyses with fewer controls, and were able to demonstrate that this had a minimal impact on the findings.

We have demonstrated how a matched nested case-control design can be embedded within an RCT to identify credible associations in a secondary analysis of clinical trial data where the exposure of interest was not randomised. We planned this study after the clinical trial data had already been collected, but it could have been built in seamlessly as a SWAT (Study Within A Trial) during the trial design phase, to ensure that all relevant data were collected in advance with minimal effort. This method has several advantages over a standard case-control design and offers the potential to make reliable inferences in scenarios where unethical or practical issues preclude the use of an RCT. Moreover, because of the flexibility of the methodology in terms of the design and analysis, the matched nested case-control design could reasonably be applied to a wide range of challenging research questions. There is an abundance of high quality large prospective studies and clinical trials with well characterised cohorts, in which this methodology could be applied to investigate causal relationships, adding considerable value for money to the original studies.

Availability of data and materials

ADEPT trial data are available upon reasonable request, subject to the NPEU Data Sharing Policy.


Abnormal Doppler Enteral Prescription Trial

  • Randomised controlled trial

Necrotising enterocolitis

Continuous positive airway pressure

Umbilical artery catheter

Umbilical venous catheter

Study within a trial

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This work was presented at the International Clinical Trials Methodology Conference (ICTMC) in 2019 and the abstract is published within Trials [ 22 ].

This work was supported by Action Medical Research [Grant number GN2506]. The funder had no role in study design, data collection and analysis, decision to publish, or preparation of the manuscript.

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Nottingham Clinical Trials Unit, University of Nottingham, Nottingham, UK

Christopher Partlett

National Perinatal Epidemiology Unit, Nuffield Department of Population Health, University of Oxford, Oxford, UK

Christopher Partlett, Alison Leaf, Edmund Juszczak & Louise Linsell

University Surgery Unit, Faculty of Medicine, University of Southampton, Southampton, UK

Nigel J. Hall

Department of Child Health, Faculty of Medicine, University of Southampton, Southampton, UK

Alison Leaf

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NH, AL, EJ and LL conceived the project. CP performed the statistical analyses under the supervision of LL and EJ. CP and LL drafted the manuscript and EJ, AL and NH critically reviewed it. All authors were involved in the interpretation of results. The author(s) read and approved the final manuscript.

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Correspondence to Christopher Partlett .

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Supplementary information

Additional file 1..

Table A1 Association between exposures and the development of Severe NEC. Each case is matched to 4 controls with the same sex and the smallest distance in terms of the Malhalanobis distance based on gestational age and birthweight.

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Partlett, C., Hall, N.J., Leaf, A. et al. Application of the matched nested case-control design to the secondary analysis of trial data. BMC Med Res Methodol 20 , 117 (2020). https://doi.org/10.1186/s12874-020-01007-w

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  • Preterm infants
  • Neonatology
  • Statistical methods
  • Nested case-control

BMC Medical Research Methodology

ISSN: 1471-2288

bias in nested case control study

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Interpreting Epidemiologic Evidence: Connecting Research to Applications (2nd edn)

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8 Selection Bias in Case-Control Studies

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In cohort studies, sampling of study participants is independent of the outcome. In contrast, in case-control studies participants are sampled at different rates depending on whether or not they develop the outcome of interest: typically all cases and a small sample of eligible controls are recruited. Controls in case-control study are used to estimate the distribution of exposure and confounders in the source population from which the cases are drawn. Thus, the challenge in case-control studies is to generate a sample of controls that represent the population experience that generated the cases, i.e., selecting from those who would have become identified cases in the study had they developed the disease of interest. Selection bias can be introduced when the chosen controls deviate from this ideal through a lack of correspondence between the source of cases and selected controls with respect to calendar time, health care seeking behavior, or other attributes. Tools for evaluating the potential for selection bias in case-control studies include comparing measured exposure prevalence among controls to an external population and determining whether the exposure among controls follows expected patterns, examining exposure-disease associations in relation to markers of susceptibility to bias, adjusting for markers of selection, and evaluating whether expected associations between exposure and disease can be confirmed.

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6.3 - comparing & combining case-control and cohort studies, comparison of cohort and case-control studies section  , nested case-control study design section  .

This is a case-control study within a cohort study. At the beginning of the cohort study, (t0), members of the cohort are assessed for risk factors. Cases and controls are identified subsequently at time t1. The control group is selected from the risk set (cohort members who do not meet the case definition at t1.) Typically, the nested case-control study is less than 20% of the parent cohort.

Advantages of nested case-control

  • Efficient – not all members of the parent cohort require diagnostic testing
  • Flexible – allows testing of hypotheses not anticipated when the cohort was drawn (at t0)
  • Reduces selection bias – cases and controls sampled from the same population
  • Reduces information bias – risk factor exposure can be assessed with an investigator blind to case status


  • Reduces power (from parent cohort) because of reduced sample size by 1/(c+1), where c = number of controls per case

Nested case-control studies can be matched, not matched, or counter-matched. Matching cases to controls according to baseline measurements of one or several confounding variables is done to control for the effect of confounding variables.

A counter-matched study, in contrast, is when we matched cases to controls who have a different baseline risk factor exposure level. The counter-matched study design is used to specifically assess the impact of this risk factor; it is especially good for assessing the potential interaction (effect modification!) of the secondary risk factor and the primary risk factor. Counter-matched controls are randomly selected from different strata of risk factor exposure levels in order to maximize variation in risk exposures among the controls. For example, in a study of the risk for bladder cancer from alcohol consumption, you might match cases to controls who smoke different amounts to see if the effect of smoking is only evident at a minimum level of exposure.

Example of a Nested Case-Control Study: Familial, psychiatric, and socioeconomic risk factors for suicide in young people: a nested case-control study . In a cohort study of risk factors for suicide, Agerbo et al. (2002), enrolled 496 young people who had committed suicide during 1981-97 in Denmark matched for sex, age, and time to 24,800 controls. Read how they matched each case to a representative random subsample of 50 people born the same year!

Case-Cohort Study Design Section  

A case-cohort study is similar to a nested case-control study in that the cases and non-cases are within a parent cohort; cases and non-cases are identified at time t1, after baseline. In a case-cohort study, the cohort members were assessed for risk factors at any time prior to t1. Non-cases are randomly selected from the parent cohort, forming a subcohort. No matching is performed.

Advantages of Case-Cohort Study:

Similar to nested case-control study design:

  • Efficient– not all members of the parent cohort require diagnostic testing
  • Flexible– allows testing hypotheses not anticipated when the cohort was drawn (t0)
  • Reduces selection bias – cases and non-cases sampled from the same population
  • Reduced information bias – risk factor exposure can be assessed with an investigator blind to case status

Other advantages, as compared to nested case-control study design:

  • The subcohort can be used to study multiple outcomes
  • Risk can be measured at any time up to t1  (e.g. elapsed time from a variable event, such as menopause, or birth)
  • Subcohort can be used to calculate person-time risk

Disadvantages of Case-Cohort Study:

As compared to nested case-control study design  –  Increased potential for information bias because subcohort may have been established after t0 exposure information collected at different times (e.g. potential for sample deterioration)


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    The study design is prone to recall bias, as described in a previous question.6 Recall bias is the systematic difference between cases and

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    More on" biased selection of controls for case-control analyses of cohort studies". Biometrics. 1986;42(2):293–9. Lubin JH, Gail MH. Biased

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    randomised controlled trial. However, its design resembled a modem, nested case-control ("case- cohort") study, rather than a randomised controlled trial.

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