Thomas

R Kirkwood

Simon Cousens
email: simon.cousens@lshtm.ac.uk

Hargreaves

Bonell

Kirkwood Br

Alternatives to randomisation in the evaluation of public-health interventions: statistical analysis and causal inference

published or not. The documents may come

2

Abstract

Background

In non-randomised evaluations of public-health interventions statistical methods to control confounding will usually be required. We summarise a variety of approaches to the control of confounding, highlighting key issues and the assumptions on which these methods are based.

Method

Explanatory review.

Results

To control confounding, standard stratification and regression techniques will often be appropriate but propensity scores may be useful where many confounders need to be controlled and data are limited. All these techniques require that key putative confounders are measured accurately. Instrumental variables offer, in theory, a solution to the problem of unknown or unmeasured confounders but identifying an instrument which meets the required conditions will often be challenging. Obtaining measurements of the outcome variable in both intervention and control groups before the intervention is introduced allows balance to be assessed, and these data may be used to help control confounding. However, imbalance in outcome measures at baseline poses challenges for the analysis and interpretation of the evaluation, highlighting the value of adopting a design strategy that maximizes the likelihood of achieving balance. Finally, when it is not possible to have any concurrent control group, making multiple measures of outcome pre-and post-intervention can enable the estimation of intervention effects with appropriate statistical models.

Conclusion

For non-randomised designs careful statistical analysis can help reduce bias by confounding in estimating intervention effects. However, investigators must report their methods thoroughly and be conscious and critical of the assumptions they must make whenever they adopt these designs.

Alternatives to randomisation in the evaluation of public-health interventions: statistical analysis and causal inference

Introduction

In our previous paper, we discussed barriers to randomised controlled trials (RCTs) of public-health interventions and suggested alternative design strategies. [START_REF] Bonell | Evaluating the effects of publichealth interventions: barriers to randomized trials and alternative options[END_REF] In this paper, we discuss the statistical analysis of data from non-randomised evaluations, dealing particularly with confounding. We outline key issues and options available when planning analyses of these data. In practice, the most appropriate statistical approach will differ from case to case, but transparent description of the design and analysis process is essential [START_REF] Jarlais | Improving the reporting quality of nonrandomized evaluations of behavioral and public health interventions: the TREND statement[END_REF][START_REF] Von Elm | The Strengthening the Reporting of Observational Studies in Epidemiology (STROBE) statement: guidelines for reporting observational studies[END_REF], as for RCTs [START_REF] Altman | Better reporting of randomised controlled trials: the CONSORT statement[END_REF].

Causal effects and confounding in non-randomised evaluations of public-health interventions

Evaluations of public-health interventions aim to estimate the causal effect of an intervention by which we mean a quantitative measure of the difference between the level of the outcome had everybody in the population of interest been exposed and the level of the outcome had everybody been unexposed. Readers are referred to [START_REF] Hernan | A definition of causal effect for epidemiological research[END_REF] for a fuller discussion of causal effects in epidemiology. [START_REF] Hernan | A definition of causal effect for epidemiological research[END_REF] Our emphasis on public-health interventions also implies we are most concerned with estimating overall (populationlevel) effects of intervention strategies, combining direct and indirect effects. [START_REF] Halloran | Direct and indirect effects in vaccine efficacy and effectiveness[END_REF] RCTs aim to achieve balance between treatment and non-treatment groups, meaning that these groups are alike with regard to all factors that might influence the outcome measure (both known and unknown), other than exposure to the intervention of interest. RCTs achieve balance by using chance to determine which people or units receive an intervention, and by applying this process many times over (i.e. allocating many units to the two groups). [START_REF] Hill | The Environment and Disease: Association or Causation?[END_REF] Most non-RCT designs also seek to achieve balance. [START_REF] Bonell | Evaluating the effects of publichealth interventions: barriers to randomized trials and alternative options[END_REF] Nevertheless, imbalance is more likely with these designs and consequently they risk generating a confounded effect estimate: one that mixes the effect of the intervention with other causal effects. [START_REF] Rothman | Modern Epidemiology[END_REF] Consider a study to evaluate the effect of a radio soap-opera designed to encourage contraceptive use in Nepal using data collected from over 8,000 women in a crosssectional survey (see box 1 in our previous paper). [START_REF] Bonell | Evaluating the effects of publichealth interventions: barriers to randomized trials and alternative options[END_REF][START_REF] Hutchinson | Advanced methods for evaluating the impact of family planning communication programs: evidence from Tanzania and Nepal[END_REF] The authors compared contraceptive use among women who reported listening to the programme in the previous six months with that among women who did not. An unadjusted analysis found that the prevalence of contraceptive use was 12% higher among listeners than non-listeners (Table 1). However, it would be premature to conclude that this reflects an intervention effect. While this study suffered from many potential biases (as do most evaluations) we highlight here the issue of confounding. For example, level of education might differ between those who did and did not listen to the soap-opera, and might also, independently, influence contraceptive use (Figure 1). Of course, educational level is only one of many potential confounders, and a more complex causal diagram than Figure 1 could be drawn to help identify other variables that should be controlled. [START_REF] Greenland | Causal diagrams for epidemiologic research[END_REF] Statistical methods for controlling confounding

(i) Stratification and regression

In the traditional approach to controlling confounding, women would be grouped ("stratified") according to their educational level, for example "none", "attended primary school" and "completed primary school". The association between intervention and outcome is examined within each group. Any association within groups cannot be due to confounding by educational status because women in each group have the same level of education, assuming this is correctly measured. If the intervention effect is approximately the same in all sub-groups, a weighted average of the stratum-specific estimates provides an adjusted effect estimate free of confounding by that variable.

Regression modelling can include multiple confounding factors as explanatory variables [START_REF] Kirkwood | Essential Medical Statistics[END_REF], and was used in the Nepal study to control 11 potential confounders, assuming no effect modification. This adjustment reduced the estimated effect from +12% to +6% (Table 1), consistent with the unadjusted estimate being partly confounded (overestimating the true effect). However, this adjusted estimate is unconfounded only if all important confounders are identified and measured accurately [START_REF] Fewell | The Impact of Residual and Unmeasured Confounding in Epidemiologic Studies: A Simulation Study[END_REF][START_REF] Kupper | Effects of the use of unreliable surrogate variables on the validity of epidemiologic research studies[END_REF]. Since we can rarely, if ever, verify this, residual confounding remains a concern.

(ii) Propensity scores

Propensity scores are another more recent approach to controlling confounding. [START_REF] Agostino | Propensity score methods for bias reduction in the comparison of a treatment to a non-randomized control group[END_REF] The following steps are taken:

1.

A regression model is used to identify factors that 'predict' exposure to the intervention. The model is used to calculate each individual's predicted probability of, rather than actual, exposure to the intervention (e.g. "listened to the soap opera").

2.

Individuals with similar propensity scores are grouped. Within each group, some individuals will actually have been exposed to the intervention and some not. Since individuals in each group had the same propensity to be exposed, the method assumes that actual exposure within these groups was random.

3.

Stratified analysis can compare outcomes between exposed and unexposed individuals within each propensity-score group and by including the propensity score group in regression analysis it is possible to obtain an unconfounded estimate of the intervention effect.

Alternatively, each exposed individual may be matched with an unexposed individual with the same or similar propensity score and the analysis restricted to these pairs.

When used in the Nepal study, this approach yielded an effect-size estimate of a 9% increase in contraceptive use. Unfortunately, no details were provided of the variables used to estimate the propensity scores though this choice may affect the estimate obtained. Future evaluations adopting this approach should provide these details [START_REF] Jarlais | Improving the reporting quality of nonrandomized evaluations of behavioral and public health interventions: the TREND statement[END_REF][START_REF] Von Elm | The Strengthening the Reporting of Observational Studies in Epidemiology (STROBE) statement: guidelines for reporting observational studies[END_REF].

Propensity scores are increasingly popular. [START_REF] Stürmer | A review of the application of propensity score methods yielded increasing use, advantages in specific settings, but not substantially different estimates compared with conventional multivariable methods[END_REF] One advantage is that their use can reduce the number of parameters (i.e. variables and categories within these) to be estimated in a regression model. When the number of parameters is large relative to the data available, estimates can become biased and confidence intervals unreliable. In the current example, using propensity scores rather than standard regression reduced the number of parameters from 25 to 8. In this case a model with 25 parameters should not have introduced bias, [START_REF] Peduzzi | A simulation study of the number of events per variable in logistic regression analysis[END_REF] since over 2500 women reported using contraceptives. However, in smaller evaluations or those focused on rare outcomes, propensity-score approaches can reduce such problems, [START_REF] Agostino | Propensity score methods for bias reduction in the comparison of a treatment to a non-randomized control group[END_REF]17] and may be more robust than standard regression when the number of events-per-confounder is small (< 8). [START_REF] Cepeda | Comparison of Logistic Regression versus Propensity Score When the Number of Events Is Low and There Are Multiple Confounders[END_REF] Problems remain however. In practice, comparisons between regression and propensityscore methods suggest they usually yield similar results. [START_REF] Stürmer | A review of the application of propensity score methods yielded increasing use, advantages in specific settings, but not substantially different estimates compared with conventional multivariable methods[END_REF][START_REF] Shah | Propensity score methods gave similar results to traditional regression modeling in observational studies: a systematic review[END_REF][START_REF] Stukel | Analysis of observational studies in the presence of treatment selection bias: effects of invasive cardiac management on AMI survival using propensity score and instrumental variable methods[END_REF] Like standard regression methods, a propensity-score analysis faces the problem of unmeasured or poorly-measured variables since all important predictors of exposure that are causally associated with the outcome must be included. Furthermore, using statistical methods to identify 'predictors' of exposure without considering underlying causal relationships might be problematic. Investigators should not include 'predictors' which are in fact consequences of exposure, since this will lead to 'over-adjusted' models and biased effect estimates. [START_REF] Greenland | Causal diagrams for epidemiologic research[END_REF][START_REF] Hernan | Causal knowledge as a prerequisite for confounding evaluation: an application to birth defects epidemiology[END_REF] Alternatively, if multiple predictors of exposure that are not causally associated with the outcome are included, then power may be unnecessarily sacrificed since, as with other methods of controlling confounding, including multiple factors in a model can reduce power. [START_REF] Winkelmayer | Propensity scores: help or hype?[END_REF] (iii) Instrumental variables

Instrumental variables are also increasingly popular, purportedly removing the need to identify and measure all potential confounders. [START_REF] Hernan | Instruments for causal inference: an epidemiologist's dream?[END_REF][START_REF] Angrist | Identification of causal effects using instrumental variables[END_REF] This approach requires an "instrument" that meets the following conditions (Figure 2):

1.
It is a cause or proxy for a cause of exposure to the intervention;

2.
It is not a cause of the outcome other than through the intervention; and 3. It is not associated with any unmeasured confounders of concern in the study population.

Identifying an instrument that satisfies these conditions allows us to generate an unconfounded estimate of the intervention effect ('effect A' in Figure 2), by comparing the magnitude of the association between the instrument and the outcome ('effect C')

with that between the instrument and exposure to the intervention ('effect B'). In the case of the Nepal example, the intervention effect is estimated by dividing the effect (risk difference) of the instrument on the outcome by the effect (risk difference) of the instrument on the exposure. The precise manner in which estimates are calculated differs depending on the situation. [START_REF] Hernan | Instruments for causal inference: an epidemiologist's dream?[END_REF][START_REF] Martens | Instrumental variables: application and limitations[END_REF] Instrumental-variable analysis may provide different estimates of treatment effect to standard or propensity-score methods. [START_REF] Stukel | Analysis of observational studies in the presence of treatment selection bias: effects of invasive cardiac management on AMI survival using propensity score and instrumental variable methods[END_REF] In the Nepal example, "listens to radio weekly" was used as an instrument (see figure 2). This analysis suggested an 8.5%

increase in contraceptive use associated with the intervention. However, we must question whether conditions 2 and 3 were met. First, listening to the radio weekly (including other programmes) could conceivably have a direct effect on contraceptive practices (violating 2). Second, important unmeasured confounders (e.g. social and cultural factors) might also be associated with this instrument (violating 3). This illustrates that it is often difficult to identify an appropriate instrument. Furthermore, we can never empirically verify the conditions required for a valid instrument. Consequently, "the fundamental problem of causal inference from observational data -the reliance on assumptions that cannot be empirically verified -is not solved but simply shifted to another realm". [START_REF] Hernan | Instruments for causal inference: an epidemiologist's dream?[END_REF] Finally, even if all three conditions above are met, if the correlation between the instrument and the intervention is not strong (the instrument is "weak"), the standard error of the intervention effect will be large and the confidence interval for the effect will be wide. [START_REF] Newhouse | Econometrics in outcomes research: the use of instrumental variables[END_REF] (iv) Using pre-intervention measures of the outcome variable in analysis

In both randomised and non-randomised evaluations, obtaining measures of the outcome variable prior to the introduction of the intervention can be useful to explore balance.

These data can also be used to control confounding since they reflect the prior influence of multiple factors that influence the outcome in the absence of intervention. The data can be incorporated into analysis in two ways:

1. Treat them in the same way as other potential confounders and fit a regression model in which the pre-intervention measure of the outcome is included alongside other potential confounders.

2. Calculate the change in the outcome and base the analysis on the difference in the changes in the two groups.

If intervention and control groups are similar with respect to baseline measures of the outcome (i.e. there is balance), or where small differences arise by chance (as could also happen in an RCT), both approaches provide unbiased estimates of the intervention effect but regression will provide a more precise estimate and is therefore preferred. [START_REF] Senn | Change from baseline and analysis of covariance revisited[END_REF] However, when non-random allocation results in two groups which are drawn from two different populations, and hence are unbalanced at baseline, the two approaches can give contradictory results. This has been described as "Lord's paradox" and was first identified in the context of individual-level data. [START_REF] Senn | Change from baseline and analysis of covariance revisited[END_REF][START_REF] Lord | A Paradox in the Interpretation of Group Comparisons[END_REF][START_REF] Wainer | Two statistical paradoxes in the interpretation of group differences: illustrated with medical school admission and licensing data[END_REF] To illustrate this paradox with an example relevant to our purposes, consider a hypothetical cluster-allocated, nonrandomised study of an intervention aiming to lower mean systolic blood pressure (MSBP) among individuals in workplaces by influencing exercise and smoking (100 intervention, 100 control sites). Intervention allocation was non-random, being determined by stakeholder meetings to identify which workplaces received the intervention. [START_REF] Bonell | Evaluating the effects of publichealth interventions: barriers to randomized trials and alternative options[END_REF] This resulted in a systematic imbalance in MSBP between the two arms at baseline (intervention 120mmHg, control 115mmHg). Following intervention, measures of MSBP were taken from individuals in all workplaces. MSBP did not change between baseline and follow-up in either the control or intervention workplaces.

In this situation, because blood pressure differed between the groups (was unbalanced) to begin with, regression analysis can incorrectly suggest that there was an effect of the intervention in some situations, while an analysis of change in the outcome does not. [START_REF] Senn | Change from baseline and analysis of covariance revisited[END_REF][START_REF] Lord | A Paradox in the Interpretation of Group Comparisons[END_REF][START_REF] Wainer | Two statistical paradoxes in the interpretation of group differences: illustrated with medical school admission and licensing data[END_REF] Here we offer one suggestion for how this paradox might occur and reflect on guidance for evaluators in this situation. Figure 3 shows the results of two simulations of the experiment with pre-intervention MSBP plotted against MSBP post-intervention for all intervention and control workplaces. In Figure 3a, we assume that MSBP was measured "perfectly". Over 1000 simulations there was no evidence for a difference between the groups from either regression analysis or analysis of changes. However, when we allowed "noise" in the baseline measurements of MSBP (Figure 3b), there was evidence of a difference between the groups in regression analysis but not change-scores.

Our simulation assumed that each individual had the same true underlying systolic blood pressure at both baseline and follow-up, i.e. we assume no real change in either group, but that at each time-point there was independent random measurement error. Our simple simulation suggests that one possible explanation for paradoxical findings when comparing an analysis of changes with a regression analysis is that "noise" results in dilution of the association between pre-and post-intervention measures as identified by linear regression. This is known as regression-dilution bias. [START_REF] Frost | Correcting for regression dilution bias: comparison of methods for a single predictor variable[END_REF] This phenomenon reduces the gradient of the regression lines in Figure 3b compared to Figure 3a. The regression lines for each group are consequently shallower, but are also centred on different means (because of the baseline imbalance) resulting in a vertical gap between the two lines. In regression analysis, this gap is equivalent to the estimated parameter for intervention effect, and might then be incorrectly interpreted in this way.

Further research is necessary to characterise the statistical properties associated with this phenomenon; we have offered only a simplified illustration. Such work is necessary because this situation might plausibly arise in non-randomised evaluations of publichealth interventions. For example, we identified an ongoing evaluation of the impact of introducing youth-centres and 'adolescent-friendly' clinics on HIV prevalence among 15-24 year-olds in South-African communities. The centres were purposively placed in disadvantaged areas for strategic purposes. [START_REF] Pettifor | A community-based study to examine the effect of a youth HIV prevention intervention on young people aged 15-24 in South Africa: results of the baseline survey[END_REF] The evaluation design aims to compare future HIV prevalence through surveys in 11 youth-centres, 11 clinics and 11 control sites but baseline HIV prevalence was higher in areas where youth-centres were placed (15.7%) than controls (13.8%: adjusted OR = 1.41 95% CI 0.96, 2.07). [START_REF] Pettifor | A community-based study to examine the effect of a youth HIV prevention intervention on young people aged 15-24 in South Africa: results of the baseline survey[END_REF] It is inevitable that there is imprecision in these site-specific estimates since they are based on a sample of the population. Given this imbalance at baseline, a future regression analysis using data from a new sample post-intervention is likely to be biased by the regression-dilution bias illustrated above. However, for change-scores to produce a valid estimate of the intervention effect, we must assume that the intervention has a constant additive effect regardless of the level at baseline on whatever scale the analysis is performed (for example, log (odds) in the case of logistic regression). The key message of Lord's paradox is, therefore, that when non-randomised intervention and control groups are unbalanced at baseline, any attempt at causal inference will be fraught with difficulty. [START_REF] Senn | Change from baseline and analysis of covariance revisited[END_REF][START_REF] Wainer | Two statistical paradoxes in the interpretation of group differences: illustrated with medical school admission and licensing data[END_REF] (

v) Imbalance and inference when the number of units studies is small

Public-health interventions are often delivered to 'clusters' of people and for practical reasons the number of clusters included in an evaluation is sometimes small. [START_REF] Bonell | Evaluating the effects of publichealth interventions: barriers to randomized trials and alternative options[END_REF] Cluster allocation must be appropriately taken into account in analyses, and this is relevant to both randomised and non-randomised designs. [START_REF] Cornfield | Randomization by group: a formal analysis[END_REF] Low statistical power in such studies, including those where large numbers of individuals but only a small number of clusters are enrolled, is a major barrier to statistical inference. We do not seek to review this issue here, other than to identify that allocation of a small number of units may also be a reason why imbalance might arise in non-randomised evaluations and thus indicate the need for control of confounding. However, many relevant statistical methods require additional assumptions when cluster numbers are low. We thus re-iterate the more general point that while in-depth studies of interventions delivered in a few study units can provide valuable information on process and provide some forms of evidence to inform publichealth decision-making [START_REF] Victora | Evidence-based public health: moving beyond randomized trials[END_REF], they are highly constrained in their capacity to provide quantitative estimates of intervention effect.

(vi) Time-series studies

When it is not possible to recruit a concurrent comparison group it may instead be possible to compare each unit pre-and post-intervention. However, once again, a "fair comparison" should be made. The before/after approach, and more sophisticated variants of this in which multiple measures of outcome are made over time, controls for sources of confounding that are static over time but not time-varying factors such as maturational, seasonal or secular trends.

"Interrupted time-series analysis" requires data on multiple measures of the outcome preand post-intervention. [START_REF] Shadish | Quasi-experiments: interrupted time-series designs. Experimental and Quasi-Experimental Designs for Generalized Causal Inference[END_REF] The following steps are taken:

1) The extent of variation in the outcome over time due to factors other than the intervention (e.g. seasonal trends) [START_REF] Biglan | The value of interrupted time-series experiments for community intervention research[END_REF] is estimated statistically.

2) A statistical model is used to predict the "expected" outcome at the end of the intervention period had the intervention not been delivered.

3) This "expected value" is compared with the "observed" post-intervention level to determine the intervention "effect".

For example, the effect of introducing pneumococcal conjugate vaccine (PCV-7) for infants in the USA was evaluated by examining monthly pneumonia admissions (see previous paper, box 1). [START_REF] Bonell | Evaluating the effects of publichealth interventions: barriers to randomized trials and alternative options[END_REF][START_REF] Grijalva | Decline in pneumonia admissions after routine childhood immunisation with pneumococcal conjugate vaccine in the USA: a time-series analysis[END_REF] There were significant seasonal variation in trends in admission (Figure 4). An expected admission rate at the end of the intervention period was obtained by extrapolating available trend data after modelling seasonal fluctuations.

The analysis found that the seasonally-corrected admission rate by December 2004 was 39% lower than the expected rate (95% CI 22%-52%) providing an estimate of the effect of PCV-7 (Figure 4a).

Interrupted-time-series analysis provides better estimates than simple before/after studies as long as putative time-varying confounding factors are measured and modelled. [START_REF] Clancy | Effect of air-pollution control on death rates in Dublin, Ireland: an intervention study[END_REF] Acute effects of rapid introduction of an intervention are generally easiest to differentiate from other sources of variation in time-series analyses. [START_REF] Shadish | Quasi-experiments: interrupted time-series designs. Experimental and Quasi-Experimental Designs for Generalized Causal Inference[END_REF] Difficulties arise if an intervention is implemented gradually or has a long latent interval before exerting effect (e.g. the effect of anti-smoking campaigns on lung-cancer rates). A challenge also arises in deciding how complicated a trend to allow for in estimating expected values postintervention. Non-linear trends can be modelled and provide better control of confounding, but require data for many time-points and may result in less-precise effect estimates. Furthermore, even after modelling trends and allowing for seasonality, there may be auto-correlation between outcome levels at adjacent time-points. [START_REF] Perez | An interrupted time series analysis of parenteral antibiotic use in Colombia[END_REF] This auto-correlation can lead to over-estimating the precision of intervention effects and provide confidence intervals that are too narrow. For continuous outcomes, there are techniques available to take account of this; for counts, a little ingenuity is required. [START_REF] Brumback | Transitional regression models, with application to environmental time series[END_REF]

Conclusion

Non-randomised evaluations are essential to inform public-health decision making where there are clear barriers to the conduct of RCTs. Over two papers, we have discussed design and analysis choices in order to ensure a "fair comparison" is made. Confounding, however, remains a major concern in these studies and investigators will face more complex problems even than those we have discussed here such as dealing with covariates that change over time. [START_REF] Cole | Effect of highly active antiretroviral therapy on time to acquired immunodeficiency syndrome or death using marginal structural models[END_REF] Evaluators and analysts have various options to consider but must make careful, informed choices that fit their context. We hope to have aided these choices. Most importantly, as we and others have stressed, investigators should transparently outline the steps taken in design and analysis so that others can judge the value of the estimates produced.

. Simulated data illustrating possible mechanism for "Lord's paradox". The vertical distance between the two regression lines corresponds to the "intervention effect" estimate obtained from regression. In figure 3a, with no "noise" in the baseline measure, this suggests no intervention effect, consistent with the analysis of change-scores. In figure 3b, with "noise" in the measurements, regression suggests an intervention effect. (a)

Details of simulation: Using STATA version 10, a simulated population of 100 intervention clusters were drawn from a sampling distribution with mean of 120, and standard deviation of 3 and 100 control clusters were drawn from a population with mean 115, standard deviation 3 to represent baseline values. A standard deviation of 3mmHg in cluster level mean SBPs could plausibly arise in an evaluation -for example if the standard deviation of individual blood pressure values in each population was 18mmHg and the number of individuals enrolled in each cluster was 36. Follow up measures simulating random variation over time but no intervention effect (Figure 3a) were simulated by adding an additional random value (mean 0, standard deviation 3) to each baseline value. "Noise" at baseline and follow up (in Figure 3b) was simulated by adding a further random value to both baseline and follow-up measurements (mean 0 , standard deviation 3). For both Figure 3a and 3b, the individual red and blue points represent the cluster-level mean values from a single simulation, while the lines from regression represent the results of 1000 repeated simulations of the experiment. In Figure 3a with no noise the black line indicates that the two regression lines are coincident; in Figure 3b the red and blue lines are separated by a distance of 2.5, representing the estimated average "intervention effect" in regression analysis, and illustrating one possible mechanism for Lord's paradox.

What we already know on this subject

Non-randomised evaluations of public health interventions are more likely than randomised designs to suffer from imbalance between intervention and control groups.

Consequently they risk generating confounded effect estimates that mix the effect of the intervention with other causal effects. A variety of statistical approaches are available to minimise confounding but existing reviews have not discussed these in a way that can help guide the planning of evaluations of public health interventions where randomisation is not possible.

What this paper adds

Like regression and stratification techniques, propensity scores require that key putative confounders are measured accurately, but may be particularly useful where many confounders need to be controlled and data are limited. Instrumental variables offer, in theory, a solution to the problem of unknown or unmeasured confounders but identifying a valid instrument will often be challenging. Outcome measures taken at baseline can be used in analysis but imbalance poses complex challenges for analysis and interpretation.

Finally, time-series analysis can enable the estimation of intervention effects with appropriate, but complex, statistical models.

Figure 1 .

 1 Figure 1. Simple causal diagram of potential causal effects and links between exposure

Table 1 .

 1 Results of an evaluation of a family-planning communication intervention in Causal diagram indicating the conditions under which a variable (the "instrument") will enable the investigator to control unmeasured confounding variables

	Nepal +
		Group	Estimated effect of the intervention
		Not	Listened to	Unadjusted	Including	Using	Using
		listened to	soap opera	analysis	potential	propensity	"listens to
		soap opera			confounders in regression	scores approach ^	the radio weekly" as
					model *		an
							instrument
	Current use	31%	43%	+12%	+6.2%	+9.2%	+8.5%
	of a modern
	contraceptive
	method

Notes on table:

+ The data on which these analyses are based are downloadable on request from http://www.measuredhs.com/.

* Probit regression, a statistical approach from the same family as logistic and linear regression that are more commonly used in public-health, was used to estimate risk differences as presented in the table. The principles we discuss apply equally to other regression methods. Variables included in the model as confounders were: woman's age, woman's educational level, household asset index, religion, lives in rural area, visited by family-planning worker in past 12 months, currently employed, number of living children, husband's education, watches television weekly, listens to radio weekly. ^ No information provided on variables used to calculate propensity score

Figure 2.

Acknowledgments

We would like to thank those who attended a symposium on evaluating public-health interventions convened by the London School of Hygiene and Tropical Medicine on 6 th November 2006 for contributing insights and thus informing the development of this paper.

Tables and Figures

Conflict of interest and funding

No authors declare any conflicts of interest regarding this paper. The work was undertaken unfunded. JH is supported by an MRC/ESRC interdisciplinary postdoctoral fellowship.

Ethics

Since the article is based on a review of existing literature, there was no requirement to seek ethical review or human subjects' informed consent to participate.


Merel Schuring

Johan Mackenbach

Toon Voorham

PhD Alex Burdorf
email: a.burdorf@erasmusmc.nl

The effect of re-employment on perceived health

Background: The relationship between unemployment and poor health has been well established. Unemployment causes poor health and poor health increases the probability of unemployment.

Methods: A prospective study with 6 months follow-up was conducted among unemployed subjects receiving social security benefits, who were capable of full time employment and were referred to a re-employment training centre. Re-employment was defined as ending social security benefits for at least three months because of starting with paid employment.

Health related quality of life was measured by the Short Form 36 Health Survey (SF-36). A Cox Proportional Hazards analysis was used to determine the factors that predicted reemployment during follow-up. The influence of re-employment on changes in perceived health was investigated with linear regression analysis.

Results: Unemployed subjects with a poor health at baseline were less likely to return to paid employment during follow-up. Almost all dimensions of health at baseline had an influence on the likelihood of becoming employed. Among the re-employed subjects, general health, physical functioning, social functioning, vitality, mental health, bodily pain, and role-limitations due to emotional or physical problems improved, with an effect size varying from 0.11 to 0.66.

Conclusion:

This study provides evidence that re-employment leads to improvement of self-perceived health within a short time window. This suggests that labour force participation should be considered as therapeutic intervention within health promotion programmes among unemployed persons.

INTRODUCTION

The relationship between unemployment and poor health has been well established, as demonstrated by a higher prevalence of illness and disability 1, 2 and a higher mortality among unemployed people. [START_REF] Morris | Loss of employment and mortality[END_REF] The association between health and employment is bidirectional: unemployment may cause poor health (causation hypothesis), and poor health may increase the probability of unemployment (selection hypothesis).

There is evidence for the selection hypothesis. A longitudinal study among European countries showed that in the majority of European countries a perceived poor health or a chronic health problem predicted becoming or staying unemployed. [START_REF] Schuring | The effect of ill health on entering and maintaining paid employment: evidence in European countries[END_REF] A community based survey in the United Kingdom found that health related job loss had become increasingly common, especially in relation to musculoskeletal disorders and mental illness. [START_REF] Solomon | Health-related job loss: findings from a community-based survey[END_REF] A twoyear follow up study of long term unemployed Norwegians reported that health related selection to long term unemployment explained a substantial part of the excess mental morbidity among unemployed people. [START_REF] Claussen | Health and re-employment in a two year follow up of long term unemployed[END_REF] However, there is also evidence for the causation hypothesis. Various studies have shown that unemployment gave rise to health effects, especially psychological distress, depression, and reduced mental health. A review of 16 longitudinal studies concerning mental health effect of unemployment concluded that loss of employment affected mental health, but also that gaining employment improved mental health. [START_REF] Murphy | The effect of unemployment on mental health[END_REF] A British longitudinal study found that transitions from paid employment to various forms of non-employment (unemployment, long-term sick leave, maternity leave) had a negative impact on mental health. Transitions from non-employment to formal employment resulted in an improvement of mental health. The effects were felt most strongly within six months after the transition. [START_REF] Thomas | Employment transitions and mental health: an analysis from the British household panel survey[END_REF] A five-year follow up study among long-term unemployed Norwegians reported recovery of mental health after re-employment. [START_REF] Claussen | Health and re-employment in a five-year follow-up of long-term unemployed[END_REF] "Work, matched to one's knowledge and skills and undertaken in a safe, healthy environment, can reverse the harmful effects of prolonged sickness absence or long term unemployment, and promote health, well-being and prosperity". This is the main message of the so-called Black report, which reviewed the health of Britain's working-age population [START_REF] Black | Working for a healthier tomorrow[END_REF][START_REF] Hulshof | Working for a healthier tomorrow[END_REF] In a review Waddel and Burton 12 concluded that re-employment leads to clear benefits in psychological health and some measures of well-being, although there is a dearth of information on physical health. A meta-analytic study of the psychological and physical well-being during unemployment also demonstrated that the bulk of research is focused on mental health outcomes, suggesting that other aspects of health need more attention. [START_REF] Mckee-Ryan | Psychological and physical well-being during unemployment: a meta-analytic study[END_REF] One study on re-employment indicated that physical as well as mental health improved among those working at one year follow-up compared to those not working. [START_REF] Pattani | Predictors of re-employment and quality of life in NHS staff one year after early retirement because of ill health; a national prospective study[END_REF] Another study also showed a positive association between gaining employment and physical functioning among older workers who were displaced. [START_REF] Gallo | Health effects of involuntary job loss among older workers: findings from the health and retirement survey[END_REF] However, both studies were among older workers who were recently displaced or early retired. It is not known whether these results can be generalized to the whole working age population with a different unemployment history.

The impact of re-employment on mental health is reported by two meta-analytic studies. [START_REF] Murphy | The effect of unemployment on mental health[END_REF][START_REF] Mckee-Ryan | Psychological and physical well-being during unemployment: a meta-analytic study[END_REF] There is limited insight into the effect size of re-employment on other dimensions of health. [START_REF] Mckee-Ryan | Psychological and physical well-being during unemployment: a meta-analytic study[END_REF] The aim of this study was to investigate the effect of reemployment on different dimensions of health within a short period after entering paid employment.

METHODS

Study population

A prospective study with 6 months follow-up was conducted among unemployed subjects.

The study population consisted of persons on social security benefits who were capable of full time employment and who were referred by the Employment Centre of the City of Rotterdam, The Netherlands, to one of the four re-employment training centres in the area for a re-employment training. Some of the participants did have chronic health problems, but were declared fit enough to be capable of full time employment after investigation by a physician, a psychologist, and an employment specialist. From December 2004 until December 2007, every week an average of 19 subjects was enrolled in the study after referral to a re-employment training centre. In total, 2754 eligible participants were included in the study. Participation in this study was voluntary. The Medical Ethics Committee of Erasmus MC provided a declaration of no objection.

Data collection

The first questionnaire was sent to prospective participants immediately after the referral to the re-employment training centre. The follow-up questionnaire was sent six months later.

The procedure of data collection was similar at baseline and follow-up. The first questionnaire was sent to the home address of the participants, followed by two reminders two respectively four weeks later. Additional actions were undertaken to include more subjects. As a large part of the study population had a non-Dutch background, the questionnaire and covering letter were translated in Turkish and send in addition to the Dutch questionnaire to subjects with a Turkish surname. If subjects of the study population needed help with filling in the questionnaire, they could get in touch with an interviewer. Subjects who did not reply to the postal questionnaire were visited by an interviewer at their home address with four attempts at different day times during a two week period. The interviewers were matched with the subjects, based on ethnicity, age, and gender, and could offer an interview in the mother tongue (Dutch, Arabic, or Turkish).

Socio-demographic variables

Socio-demographic variables, such as ethnic background, highest educational level, age, sex, and marital status were included in the questionnaire. Ethnic background of the respondent was based on the country of birth of the mother. In case the mother was born in The Netherlands, the country of birth of the father was leading. [START_REF] Cbs | Herkomst van personen; allochtonen en migratie [Country of origin of persons; migrants and migration[END_REF] Different ethnic groups were defined, based on differences in geographical and cultural distance from the Netherlands. Three ethnic minority groups were defined: 1) Turks and Moroccans, 2) Antilleans and Surinamese, and 3) a miscellaneous group with all other countries of origin. Subjects were divided into three groups according to their highest level of educational attainment. A high educational level was defined as higher vocational training or university, intermediate educational level was defined as higher secondary schooling or intermediate vocational training, and low educational level was defined as no education, primary school, lower and intermediate secondary schooling or lower vocational training.

Marital status was used to distinguish those subjects married or living together from others.

Psychological measures

Mastery was measured by the Personal Mastery Scale 17 , which consists of seven items (eg "I have little control over the things that happen to me", "There is little I can do to change many of the important things in my life"), answered on a four point Likert scale (strongly agree to strongly disagree). Average scores across items were calculated, ranging from 1 to 4, with a higher score indicating a higher level of mastery. In case three or more items were unanswered, no score was computed.

Self-esteem was measured with the Rosenberg Self-Esteem Scale [START_REF] Rosenberg | Society and the adolescent self-image[END_REF] , with 10 items (e.g., "On the whole, I am satisfied with myself", "All in all, I am inclined to feel that I am a failure"), answered on a four point Likert scale (strongly agree to strongly disagree).

Average scores across items were calculated again, ranging from 1 to 4; a higher score indicated a higher level of self-esteem. In case three or more items were unanswered, no score was computed.

Re-employment training

A re-employment training centre provided a standardized approach of a re-employment training, characterized by a broad re-orientation on employment and employability, enhancement of job search skills, and intensification of job search efforts.

Re-employment

Start and end dates of the social security benefits were registered at the Employment Centre of the City of Rotterdam, The Netherlands. In these registers, additional information about reasons for ending benefits was also administered. Re-employment was defined as leaving the social security benefit services for at least three months because of starting with paid employment, verified by the national Social Security Agency. Subjects who quitted their registration for a social security benefit for other reasons, for example moving in with a partner or moving out of the city of Rotterdam, were censored from the moment that their benefit payment was quitted by the social security services.

Health measures

Health related quality of life was measured with the Dutch version of the Short Form 36

Health Survey (SF-36). [START_REF] Ware | The MOS 36-item short-form health survey (SF-36). I. Conceptual framework and item selection[END_REF][START_REF] Van Der Zee | Het meten van de algemene gezondheidstoestand met de RAND-36: een handleiding[END_REF] Self-reported health (SRH) was measured with the first item of the SF-36 by asking subjects to rate their overall health on a five-point scale, ranging from 'excellent', very good', 'good' and 'fair' to 'poor'. Those reporting less than 'good health' were defined as having a poor health. [START_REF] Fayers | Understanding self-rated health[END_REF] The other 35 items of the SF-36 were used to calculate scores on eight dimensions: physical functioning, general health, mental health, bodily pain, social functioning, vitality, role limitation due to emotional health problems, and role limitation due to physical health problems. Scores could range from 0 to 100, with a higher score indicating a better health related quality of life.

Statistical analysis

All statistical analyses were conducted by means of the statistical package SPSS (version 15) for Windows and the level of significance was set at 0.05.

In the analyses two groups of respondents were compared, those who were still unemployed at follow-up and those who were re-employed at follow-up. The baseline characteristics of both groups were compared with the chi-square test for dichotomous data and the t-test for continuous data. Non-response to the first questionnaire and loss-tofollow up during the six months until the second questionnaire were investigated by logistic regression analysis with potential determinants; individual characteristics, perceived health, participation in re-employment training, and re-employment.

A Cox Proportional Hazards analysis was used to determine the factors that predicted re-employment during the follow-up period. The follow-up period was censored at date of re-employment. Independent factors were individual characteristics, self esteem, mastery, and the eight dimensions of the SF36. Variables were coded in such a manner that a Hazard Ratio above 1 indicates an increased likelihood of re-entering paid employment.

For each dimension of the SF36 a standardized Hazard Ratio was calculated based on an average score across items, representing the effect of an increase of one standard deviation in the average score at baseline on the likelihood of entering paid employment. Individual characteristics with a significant univariate effect on re-employment, were entered first in the multivariate model. Subsequently, the health measure with the largest goodness-of-fit in the univariate analysis was entered in the multivariate model. After that, the effect of the other measures of health were investigated for their additional effect on goodness-of-fit.

The association of re-employment with changes in perceived health was investigated with linear regression analysis. The association of re-employment with each dimension of health was adjusted for age, sex, ethnic background, education, duration on benefit, participation in a re-employment training, and also for the baseline value of the health dimension under study. For each dimension of health Cohen's d was calculated as measure of effect size by dividing the difference in health before and after re-employment by their pooled standard deviation. [START_REF] Cohen | Statistical power analysis for the behavioral sciences[END_REF]

RESULTS

Figure 1 shows that 2754 subjects were enrolled in the study after referral to a reemployment training centre. One third of the subjects (n=932) had chronic health complaints, but were declared to be fit enough to be capable of full time employment after investigation by a physician, a psychologist and an employment specialist. From the 2754 subjects who received the first questionnaire, 1829 subjects (66%) filled out and returned the questionnaire. More than two third of the respondents (70%) returned the baseline questionnaire by post, whereas almost one third of the respondents (30%) had a face-toface interview. Non-response was statistically significantly higher among younger subjects and men.

The response at follow-up was 53% (965/1829). Loss-to-follow up was statistically significantly higher among younger subjects, men, and subjects of non-Dutch origin, but not related to marital status, employment history, duration on benefit, or health at baseline. Subjects who had started with a re-employment training (n=461) were less often lost to follow up (OR=0.8, 95% CI 0.7-1.0), whereas subjects who had returned to paid employment (n=123) were more often lost to follow up (OR=1.9, 95% CI 1.3-2.7).

However, among those who returned to paid employment, health at baseline did not differ significantly between non-respondents (n=76) and respondents (n=47) at follow-up.

Table 1 shows the characteristics of the respondents to the first questionnaire. The mean age of respondents was 39.7 (sd 9.5) years, 49% was man, 57% had a low level of education, 75% belonged to an ethnic minority group, and 43% received social security benefits for more than five years. During the follow-up period 30% of the respondents had started with a re-employment training. Figure 2 shows that health at baseline was better among subjects who returned to paid employment during the follow-up period. All dimensions of health improved among re-employed subjects, whereas the health status of unemployed subjects remained unchanged.

Table 2 shows that unemployed subjects with a poor health at baseline were less likely to return to paid employment during follow-up (OR=0.39, 95% CI 0.2-0.7). All dimensions of perceived health at baseline had an influence on the likelihood of becoming employed, except for mental health. Physical functioning had the strongest influence on the likelihood of becoming employed (OR=2.76, 95% 1.8-4.3). Ethnic background, marital status, self esteem, mastery, and participating in a re-employment training were not significant in the univariate model. In the multivariate analysis, physical functioning at baseline had the strongest association with re-employment. Due to the correlations of the other health measures with physical health (general health r = 0.56, bodily pain r = 0.62, mental health r = 0.26, social functioning r=0.43, vitality r=0.41, role functioning, emotional r = 0.27, role functioning, physical r = 0.55), these measures of health did not have a significant contribution to the multivariate model including physical functioning.

Table 3 shows that among the re-employed subjects general health, physical functioning, social functioning, vitality, mental health, bodily pain, and role-limitations due to emotional or physical problems improved during the follow-up period, with an effect size varying from 0.11 to 0.66. The largest relative improvements were observed for mental health, social functioning, and role-limitations due to emotional or physical problems, whereas physical functioning showed the smallest relative improvement. For those subjects who remained unemployed the effect sizes varied from -0.04 to 0.06, indicating that their health status remained virtually unchanged during the six months follow-up period. Participation in a re-employment training was not associated with change of health status (data not shown).

DISCUSSION

Unemployed subjects with a poor health at baseline were less likely to return to paid employment during follow-up. Almost all dimensions of health at baseline had an influence on the likelihood of becoming employed. The strongest association was found between physical functioning at baseline and re-employment. Among the re-employed subjects, general health, physical functioning, social functioning, vitality, mental health, bodily pain, and role-limitations due to emotional or physical problems improved, with an effect size varying from 0.11 to 0.66. Hence, re-employment positively influenced mental health as well as physical health.

Loss to follow up was significantly higher among younger subjects, men, subjects of non-Dutch origin and subjects who had returned to paid employment. However, among those who found employment (n=123), health at baseline did not differ between nonrespondents (n=76) and respondents (n=47) at follow up. Therefore, we assume that the effects of re-employment on health were not influenced by selective loss to follow up.

Subjects who were referred to a re-employment training centre were included in the study. The policy of the Employment Centre of the City of Rotterdam was to refer everybody who was able to work and could use some help with searching for a job. Hence, subjects were not included in the study when they were not able (due to health problems)

or not obliged (due to family obligations or education) to work. In addition, recently unemployed persons who were supposed to be able to find paid employment by themselves, were not included. This may have affected the results with respect to health status and re-employment probabilities.

The re-employed workers got their jobs at different times during the follow-up period of the study. Therefore, some persons may have been back at work for much longer than others and thus, the length of exposure to the health benefits of re-employment varied amongst the re-employed sample. Unfortunately, due to the small number of persons who gained employment it is not feasible to analyse the relation between time at work and health benefits due to re-employment.

The study is based on self-reported health status. Therefore, justification bias may have influenced the present results. Respondents who were still unemployed at follow up may have reported more easily that they had a poor health than those who found paid employment in order to justify the fact that they did not find a job. [START_REF] Kapteyn | Dynamics of work disability and pain[END_REF] Due to the observational design of the study the results may have been influenced by selection bias. Subjects who found employment differed from those who stayed unemployed with respect to health at baseline and personal characteristics. These variables were adjusted for in the analysis, but there may have been other variables that influenced both health change and re-employment, e.g. motivation to work, that were not included in the analysis. However, two psychological measures that were included in the study, self esteem and mastery, did not have a significant influence on the likelihood of reemployment. In addition, these psychological measures did not influence the estimated effects of re-employment on health.

To control for the systematic differences in health at baseline between the unemployed and re-employed subjects, stratified analyses were conducted showing that reemployment resulted in an increase of health for both subjects with a poor health at baseline as well as subjects with a good health at baseline. In general, subjects with a poor health at baseline showed a larger increase in health after re-employment than subjects with a good health at baseline (data not shown).However, after finding paid employment the health status of recently re-employed subjects still lagged the health status of long-term employed persons. [START_REF] Schuring | Ethnic differences in unemployment and ill health[END_REF] Unemployed subjects with a good health were more likely to return to paid employment during follow-up. Therefore, the results of this study support the selection hypothesis. These findings are in accordance with a study of the European Community Household Panel, which found that a poor health or chronic health problem predicted staying or becoming unemployed in European countries. [START_REF] Schuring | The effect of ill health on entering and maintaining paid employment: evidence in European countries[END_REF] A two year follow up study of long term unemployed in Norway showed that health related selection to long term unemployment explained a substantial part of the excess mental morbidity among unemployed people. [START_REF] Claussen | Health and re-employment in a two year follow up of long term unemployed[END_REF] This study also showed that the health status of re-employed subjects improved, whereas the health status of unemployed subjects remained unchanged. Re-employment did not only have a positive influence on mental health, but also on physical functioning, which was in accordance with findings from two other studies [START_REF] Pattani | Predictors of re-employment and quality of life in NHS staff one year after early retirement because of ill health; a national prospective study[END_REF][START_REF] Gallo | Health effects of involuntary job loss among older workers: findings from the health and retirement survey[END_REF] Based on these finding, it seems most likely that starting with paid employment results in health improvement.

However, due to the design of the study it cannot be ruled out that it is the other way around; a change in health status may increase the likelihood of finding paid employment.

However, a review showed that an increase in health status of long term unemployed is rather unlikely. [START_REF] Janlert | Unemployment as a disease and diseases of the unemployed[END_REF] Therefore, it is assumed that the health status of participants increased shortly after re-employment, supporting the causation hypothesis. This is in congruence with findings from other studies, which found an increase in mental health status after reemployment. [START_REF] Thomas | Employment transitions and mental health: an analysis from the British household panel survey[END_REF][START_REF] Claussen | Health and re-employment in a five-year follow-up of long-term unemployed[END_REF] In the present study, an effect size of 0.66 was found for the improvement of mental health after re-employment. This result is in accordance with findings from two metaanalytic studies [START_REF] Murphy | The effect of unemployment on mental health[END_REF][START_REF] Mckee-Ryan | Psychological and physical well-being during unemployment: a meta-analytic study[END_REF] , reporting that gaining employment impacts on mental health with an effect size of 0.54 respectively 0.89. The effects on other dimensions were slightly lower, but since different dimensions of health were associated with each other it is difficult to infer that mental health seems more important than physical health. This is in accordance with the results of the Whitehall II study of civil servants, which showed that physical and mental health were correlated for participants with a low socioeconomic position. [START_REF] Sacker | Social Inequality in Physical and Mental Health Comorbidity Dynamics[END_REF] In the current study only 5 % (47/965) of the participants found paid employment within six months. This low re-employment rate is in accordance with a study among persons receiving social security benefits in the city of Amsterdam, the Netherlands, which showed that only 8% of the persons found paid employment in a two-year period from 2004-2006. [START_REF]Re-integratie -van bijstand naar werk[END_REF] The current study population is characterised by a long-term unemployment history. Long-term unemployed subjects often have much difficulty in finding paid employment, especially for those with a poor health. All participants in the study were referred to a re-employment training centre for a re-employment training. However, this reemployment training did not have a positive effect on the probability of re-employment or on the health status of participants. Therefore, other measures seem to be required to increase the chance of re-employment for long term unemployed with a poor health.

In the recent Black report on the health of the British working age population, Black appealed for changing perceptions of fitness for work. Instead of sticking to the idea that one cannot work unless 100% fit, it is recommended that a campaign should be launched to make employers, healthcare professionals and the general public aware that work is in general good for health. [START_REF] Black | Working for a healthier tomorrow[END_REF] This study provides evidence that work is indeed good for your health and, thus, work should be considered as an important part of health promotion programmes among unemployed persons. In policies for health equity public health measures are required to include persons with a poor health in the labour market and to prevent workers with ill health from dropping out of the workforce.

Competing interests: None.

Figure 1 : 20 Figure 2 :

 1202 Figure 1: Flow of participants and response at baseline and follow-up.

Table 1

 1 Characteristics of respondents to the first questionnaire (n=1829)

		Respondents
	Variable	N=1829
	Age (n -%)
	18-44 yr	1230 (67)
	45-64 yr	599 (33)
	Men (n -%)	894 (49)
	Marital status living with partner (n -%)	601 (33)
	Educational level (n -%)
	Higher and intermediate level	634 (35)
	Lower level	1049 (57)
	Missing	146 (8)
	Ethnic background (n -%)
	Native Dutch	450 (25)
	Turkish / Moroccan	448 (25)
	Antillean / Surinamese	488 (27)
	Refugee / Other immigrants	404 (23)
	Duration on social benefit (n -%)
	Less than one year	478 (27)
	Between 1 and 5 years	512 (29)
	5 years and more	759 (43)
	Started with re-employment training (n -%)	541 (30)
	Self esteem (scale 1-4: mean -sd)	2.48 (0.6)
	Mastery (scale 1-4: mean -sd)	2.89 (0.5)

Table 2

 2 The influence of individual characteristics and dimensions of self-perceived health

	among long-term unemployed persons (n=965) on the likelihood of re-employment
	(n=47) during a follow-up period of six months.
	(Cox Proportional Hazards analysis)
		Re-employment	Re-employment
		(univariate model)	(multivariate model)
		Hazard Ratio (95%CI) Hazard Ratio (95%CI)
	Higher age (>45 years)	0.40 (0.20-0.83)**	0.45 (0.19-1.10)*
	Men	2.19 (1.21-3.97)**	1.74 (0.91-3.31)
	Low educational level	0.52 (0.30-0.93)**	0.60 (0.32-1.12)
	Poor health	0.39 (0.22-0.69)**	-
	General health 1	1.57 (1.20-2.07)**	-
	Physical functioning 1	2.76 (1.80-4.24)**	2.18 (1.40-3.38)**
	Bodily pain 1	1.92 (1.42-2.60)**	-
	Mental health 1	1.19 (0.89-1.59)	-
	Social functioning 1	1.54 (1.13-2.10)**	-
	Vitality 1	1.48 (1.12-1.95)**	-
	Role functioning, emotional 1	1.44 (1.06-1.96)**	-
	Role functioning, physical 1	1.72 (1.25-2.37)**	-
	** p<0.05, * p<0.10

1 Standardized Hazard Ratio, representing the effect of an increase of one standard deviation in the average score.

Table 3 :

 3 The influence of re-employment on changes in eight dimensions of health measured by the SF-36 health questionnaire among long-term unemployed persons during a follow-up period of six months.

		Effect of re-employment	Effect size 2
		change 1 (SE)	(Cohen's d)
		(n=965)	(n=47)
	General health	+ 7.0 (2.7)**	+ 0.18
	Physical functioning	+ 9.2 (3.4)**	+ 0.11
	Bodily pain	+ 11.3 (3.6)**	+ 0.20
	Mental health	+ 11.0 (2.7)**	+ 0.66
	Social functioning	+ 14.2 (3.8)**	+ 0.32
	Vitality	+ 7.8 (2.5)**	+ 0.26
	Role functioning, emotional	+ 22.7 (6.8)**	+ 0.46
	Role functioning, physical	+ 20.0 (6.0)**	+ 0.33

Each linear regression model was adjusted for age, gender, ethnic background, education, duration on benefit, and health at baseline. 2: Effect sizes were based on the mean values of health at baseline and follow-up of the re-employed subjects

Licence statement

I (Alex Burdorf), the Corresponding Author of this article (the Contribution) has the right to grant on behalf of all authors and does grant on behalf of all authors, a licence to the BMJ Publishing Group Ltd and its licensees, to permit this Contribution (if accepted) to be published in Journal of Epidemiology and Community Health (JECH) and any other BMJ Group products and to exploit all subsidiary rights, as set out at (http://jech.bmj.com/ifora/licence.pdf).

What is already known on this subject

• The relationship between unemployment and poor health has been well established.

• Unemployment may cause poor health, and poor health may increase the probability of unemployment.

What does this study add?

• Among re-employed persons, general health, physical functioning, bodily pain, mental health, social functioning, vitality and role-limitations due to emotional or physical problems improved, with an effect size varying from 0.11 to 0.66.

• Re-employment leads to improvement of self-perceived health within a short time window.

• Socioeconomic inequalities in health can be reduced by increasing labour participation.