Self‐certification versus physician certification of sick leave for reducing sickness absence and associated costs

Johanna Kausto; Jos H Verbeek; Jani H Ruotsalainen; Jaana I Halonen; Lauri J Virta; Eila Kankaanpää

doi:10.1002/14651858.CD013098

Self‐certification versus physician certification of sick leave for reducing sickness absence and associated costs

Authors' declarations of interest

Version published: 15 August 2018 Version history

https://doi.org/10.1002/14651858.CD013098

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Abstract

This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:

To evaluate the effects of introducing, abolishing, or changing the period of self‐certification of sickness absence on:

the total or average duration (number of sickness absence days) of short‐term sickness absence periods;
the total or average number of short‐term sickness absence periods;
the associated costs (of sickness absence and (occupational) health care); and
social climate, supervisor involvement, and work load or presenteeism (Figure 1).

Background

Description of the condition

Sickness absence or sick leave can be defined as "absence from work that is attributed to sickness by the employee and accepted as such by the employer" (Whitaker 2001). Sick pay refers to the continuation of payment of the employee’s salary (or part of it) by the employer during the sickness absence. A sickness benefit is usually paid from insurance, after the employer’s obligation of sick pay has ceased (Spasova 2016). From the societal and employers' perspectives, sickness absence has a large economic impact. The incidence of sickness absence and the methods that are used to calculate the costs vary between countries; however, a conservative estimate of the average cost of sickness absence to a nation is 2.5% of GDP (Eurofound 2010).

Definitions of short‐term and long‐term sickness absence vary between studies. On one hand, long‐term sickness absence has been defined as absence exceeding 20 to 90 days or longer (Higgins 2012). On the other hand, the NICE guidance (UK) uses four or more weeks as the definition of long‐term sickness absence (Gabbay 2011; NICE 2009). A short sickness absence from work is usually a minor disturbance from the perspective of the workplace and work is often taken over by colleagues. For longer term sickness absence spells, replacements are needed and they have to be paid in addition to sick pay and the payment of sickness benefit. It can be inferred that both short‐term and longer‐term sickness absence can affect productivity and the economy of companies as well as that of the country. In this Cochrane review, we focus on short‐term sickness absence which is defined as absence of less than four weeks, based on the NICE guidelines (NICE 2009).

Description of the intervention

An important procedure in the recognition of a need for sickness absence is the certification of illness or reduced work ability by a physician. This means that, in the case of sickness and reduced work ability, an employee needs a medical certificate to be absent from work. Often, the certifying physician is a general practitioner. It has been evaluated that, in Sweden, 9% of visits at general practitioners' practices included sickness certification (Englund 2000). Internationally, there is variation in sickness certification practices. Some countries, like the Netherlands, do not use any official sickness certification procedures, and employers are free to organize sick leave procedures jointly with their employees. In other countries, there can be a period of varying length at the beginning of the sickness absence during which no medical certificate is needed. Usually the employee notifies his or her supervisor when taken ill and, consequently, this procedure is called self‐certification. The role of the supervisor may vary from merely registering the notification to actually assessing the situation before giving permission to stay at home without a medical certificate. The permitted duration of absence based on self‐certification usually ranges from one to seven days (NOSOSCO 2015; Wynne‐Jones 2008).

How the intervention might work

Sickness absence and return to work may be associated with multiple factors at the levels of the individual, work and work environment, other areas of life, features of the social insurance system, and the larger societal context. Therefore, there are several pathways (practical, attitudinal, and motivational) at various levels (individual employee, the workplace, and occupational health care) that may mediate the effect of changing the period of self‐certification of sickness absence on short‐term sickness absence and associated costs, social climate, supervisor involvement and workload or presenteeism (working while ill; Figure 1). In a Finnish survey (Hinkka 2018), the majority of participating physicians found that the insufficient availability of healthcare services in the public sector was one reason for prolonged sickness absences. The practice by which the worker has to make an appointment with the physician and the physician has to be available may also prolong sickness absence, while self‐certification practice could shorten the absence when access to health care is poor. These kinds of administrative factors may increase the duration of very short‐term sick leave. For example, if a physician certificate is required, the appointment with the physician may delay return to work due to physician availability, even if the employee felt healthy enough to return to work earlier. The physician is also likely to make a conservative assessment of the work ability of the worker to prevent presenteeism. A self‐assessment might therefore decrease the number of days absent from work, because the employee can return to work as soon as she or he feels fit to work, as no restrictions are set by a medical certificate (Pesonen 2016).

Figure 1

Logic model of the intervention

Self‐certification can be interpreted by the employee as increased decision latitude (ability to make work‐related decisions and personal control over work‐related matters), while poor decision latitude at work has been associated with increased sickness absence (Melchior 2003; Michie 2003). It is also possible that employees may interpret self‐certification as an indication of the employer's trust, which can in turn result in a stronger commitment to work, decrease in sickness absence, and positive effect on social climate in the workplace (Pesonen 2016). Social climate can be defined as a shared, distinctive, and dynamic perception of social environment that can influence behavior (Bennett 2010).

The requirement of a sickness certificate from a physician may be thought of as a means to control the use of sick leave because of the existence of a moral hazard. In economic terms, a moral hazard implies that individuals utilize sickness absence (or insurance) more than necessary to maximize their utility (Khan 2009). In fact, the moral hazard may especially apply to short sickness absence spells, because for longer spells it would be more evident that there is a medical cause for the absence. According to this logic, the requirement of a sickness certificate in the case of short‐term sickness absence would be a strong intervention to prevent the moral hazard, and changing to a self‐certification procedure would possibly lead to a moral hazard problem with an increase in short‐term sickness absence spells. On the other hand, it is possible that introducing or extending self‐certification will result in presenteeism.

In an earlier investigation, it was found that a self‐certification practice improved communication between employees and supervisors (Pesonen 2016); good communication between employees and supervisors can prevent or mitigate the possible moral hazard related to self‐certification (Nieuwenhuijsen 2004). The supervisors found that the practice of self‐certification was a useful tool in the management of well‐being at work. On the other hand, Pesonen 2016 also found that the practice of self‐certification increased supervisors' workload. However, self‐certification decreased the use of resources in occupational health care and permitted the shift of resources to preventive work.

Why it is important to do this review

For short spells of sickness absence in particular, physician certification is an expensive process due to the administrative procedures involved. In addition, physician certification is associated with considerable costs and uptake of resources that could be better used in other healthcare areas. It is also known that sickness certification practices vary a lot between physicians (Arrelöv 2005; Englund 2000; Kankaanpää 2014). Literature reviews have concluded that physicians report difficulties with the certification process (Letrilliart 2012; Wynne‐Jones 2010). However, as the role of general practitioners in sickness certification differs between countries, there may be variation regarding which aspects of the process are problematic (Winde 2012). Altogether, sickness certification involving a physician has been regarded as a burden to the employees, the employer, the healthcare system, and society (Letrilliart 2012).

Sickness certification practices vary between countries and the practice of self‐certification is not common in all countries. It is unclear whether and how sickness absence is altered when the requirements of a sickness certificate change. Potentially, self‐certification will decrease the total number of short‐term sick leave days because there will be less administrative delay with the frequently occurring shorter spells, and employees can return to work as soon as they feel that their work ability is good enough. However, it is likely that self‐certification will not influence the duration of long‐term sick leave because the medical condition will be more serious and assessment and documentation by a physician will be a natural part of healthcare procedures.

In a Swedish randomised controlled trial, it was found that postponing the requirement for a physician’s certificate from day eight until day fifteen increased the average duration of sickness absences by 6.6 percent (Hesselius 2005). A cost‐benefit analysis showed that costs of increased sickness duration exceeded the benefits from fewer medical appointments. In contrast, a Norwegian study by Mykletun 2014 showed that when the sickness certification entitlement was transferred from physicians to employees (self‐certification) for a period of one year, there was a significant decline in sickness absence. Recently, a Finnish case study of six companies indicated that changing from physician certification to a self‐certification system did not affect the total number of sick leave days (Pesonen 2016). However, short‐term absence days decreased slightly, and the researchers pointed out that there were other benefits, such as a more active role of the supervisor and a 20% to 40% decrease in physician consultations.

A literature review on rates of sickness certification suggested that the countries with the longest period of self‐certification (e.g. the UK and Sweden, with seven days) reported high overall rates of sickness certification when compared to countries with shorter self‐certification periods (e.g. Norway, with four days, and Switzerland, with three days; Wynne‐Jones 2008). However, other factors such as the existence of waiting days (i.e. the first days of sickness absence without pay, or the length of the period of sick pay), may also affect sickness absence rates. Due to the uncertainty surrounding the benefits and costs of self‐certification, it is important to conduct a systematic review to combine the findings of existing studies. As far as we know, there are no systematic reviews on the effects of different sickness certification practices on sickness absence or related costs. Systematic reviews on sick leave and sickness certification practices are needed, as they can be used in preparation of evidence‐based guidelines for healthcare.

Objectives

To evaluate the effects of introducing, abolishing, or changing the period of self‐certification of sickness absence on:

the total or average duration (number of sickness absence days) of short‐term sickness absence periods;
the total or average number of short‐term sickness absence periods;
the associated costs (of sickness absence and (occupational) health care); and
social climate, supervisor involvement, and work load or presenteeism (Figure 1).

Methods

Criteria for considering studies for this review

Types of studies

We will include randomised controlled trials, where individual employees are randomly assigned either to a group that continues with the current practice of sickness certification (by a physician or by the employee his or herself) or to a group that starts a new practice of sickness certification. The change may be from physician certification to self‐certification (or vice versa) or to a longer or shorter period of self‐certification. Legal and practical constraints will make randomisation difficult at the individual level, but it is conceivable that these constraints could be overcome by using a cluster‐randomised design in which groups of workers or whole organizations are randomly assigned to the intervention or the control group We will therefore also include cluster‐randomised controlled trials.

Because of the difficulty of performing randomised trials with this intervention, we will also consider the following observational study designs for inclusion: controlled before‐after studies (otherwise known as prospective cohort studies or quasi‐experimental studies) and interrupted time‐series studies. Given the fluctuation in sick leave indicators over time, these study designs should be able to control for trends related to factors other than the intervention. Without such caution, it would be difficult to make inferences from the results of the studies.

Controlled before‐after studies (CBAs) are easier to perform ‐ considering that the intervention is carried out at the group level ‐ while maintaining reasonable validity. We define CBA studies as prospective or retrospective studies in which measurements of the outcome are available both before and after the implementation of the intervention for both the intervention and control group, and in which the outcome is measured at the same moment in time for both groups.

Interrupted time‐series studies are studies with or without a control group in which the outcome has been measured at least three times before the intervention and at least three times after the intervention. The intervention is applied at a specific well‐defined moment in time and is supposed to have an immediate effect, a long‐term effect, or both. Because the outcome is measured several times before and after the intervention, it is possible to take time trends into account and thus make up for the lack of a control group (Ramsay 2003).

Types of participants

We will include studies that have been carried out with individual employees or insured workers. We will also include studies in which participants are at the aggregate level of organizations, companies, municipalities, healthcare settings, or general populations.

Types of interventions

We will include studies that have evaluated the effects of introducing, abolishing, or changing the period of self‐certification of sickness absence. We will include any sickness certification practice in which the employee can report sick for a certain number of days without physician certification or certification by any other healthcare professional. Self‐certification can be accepted for any disease or restricted to certain types of diseases.

We will also include studies that combine self‐certification with an intervention related to supervisor role or practices, working conditions (e.g. flexible working conditions), or terms of sickness benefit (e.g. number of waiting days), etc. (i.e. multicomponent interventions).

Types of outcome measures

Primary outcomes

The total or average duration (number of sickness absence days) of short‐term sickness absence periods.
The total or average number of short‐term sickness absence periods.

If self‐certification is restricted to certain diseases, we will also consider the outcomes only for those diseases.

We will include any type of measurement of sickness absence, such as administrative data or self‐reported data.

We will report the results of economic evaluation studies related to introducing, abolishing, or changing the period of self‐certification of sickness absence. We will evaluate costs from the societal, employer's, and the employee's perspectives. The cost‐related outcome measures are:

the costs of short‐term sickness absence per employee (average within the organization);
the total cost of short‐term sickness absence
the costs of (occupational) health care; and
changes in productivity.

We will categorise the outcome measurements according to three follow‐up times: up to three months, between three and six months, and six months or longer.

Secondary outcomes

We will also include studies that have measured a change in the social climate, supervisor involvement, and work load or presenteeism, regardless of whether they report any of the primary outcomes.

Search methods for identification of studies

Electronic searches

We will conduct a systematic literature search to identify all published and unpublished studies that can be considered eligible for inclusion in this review. We will adapt the search strategy we developed for Ovid Medline (see Appendix 1) for use in the other electronic databases. We will impose no restriction on language of publication. We will arrange for the translation of key sections of potentially eligible non‐English language papers or we will arrange that people who are proficient in the publications' languages fully assess them for potential inclusion in the review as necessary.

We will search the following electronic databases from inception to present for identifying potential studies.

Cochrane Central Register of Controlled Trials (CENTRAL) in the Cochrane Library.
MEDLINE Ovid (Appendix 1).
SCOPUS.
PsycINFO Ovid.
EBM Reviews Ovid.
CINAHL EBSCOhost.
EconLit Pro Quest.
EBSCO Business Source Elite (EBSCOhost).
EconPapers.
NIOSHTIC OSH‐UPDATE.
NIOSHTIC‐2 OSH‐UPDATE.
HSELINE OSH‐UPDATE.
CISDOC OSH‐UPDATE.

We will also conduct a search of unpublished trials on ClinicalTrials.gov (www.ClinicalTrials.gov) and the WHO trials portal (www.who.int/ictrp/en/). We will utilize Google Scholar for exploratory searches.

Searching other resources

We will check reference lists of all primary studies and review articles for additional references. We will contact experts in the field to identify additional unpublished materials. We will also search web sites of social security organizations such as the International Social Security Association (ISSA) for potential studies. We will additionally search for unpublished studies and studies in languages other than English.

Data collection and analysis

Selection of studies

We will conduct the selection of eligible studies in two stages by using the study screening tool Covidence. First, pairs of review authors (JK, JHV, JHR, JIH, LJV) will independently screen titles and abstracts of all potentially relevant studies identified by our systematic search. The same authors will code them as 'include' (eligible or potentially eligible/unclear) or 'exclude'. At this stage we will exclude all references that clearly do not fulfil our inclusion criteria or that do fulfil our exclusion criteria. We will discuss any differences of opinion regarding references coded 'include' until we reach a consensus. At the second stage, we will retrieve the full‐text study reports or publications and two review authors (JK, JIH) will independently assess the full‐text and identify studies for inclusion. At this stage we will include all references that fulfil our inclusion criteria. We will record reasons for exclusion of the ineligible studies assessed as full‐texts so that we can report these in a 'Characteristics of excluded studies' table. We will resolve any disagreement through discussion or, if required, we will consult a third review author (JHR). We will identify and exclude duplicates and collate multiple reports of the same study so that each study rather than each report is the unit of interest in the review. We will record the selection process in sufficient detail to complete a PRISMA study flow diagram.

Should our systematic searches identify studies conducted by authors of this review, we will make sure to avoid conflict of interest by having all decisions concerning inclusion and exclusion made by review authors who were not involved with the study.

We will also seek to obtain further information from the authors when a paper is found to contain insufficient information for reaching a decision on eligibility.

We will rerun our systematic searches for trials every two years to enable updating the review accordingly.

Data extraction and management

We will use a data collection form that has been piloted on at least one study in the review to extract study characteristics and outcome data. One review author (JK) will extract the following study characteristics from the included studies.

Methods: study design, total duration of study, study location, study setting, withdrawals, and date of study.
Participants: N, mean age or age range, sex/gender distribution, occupation, type of work and branch of industry, and inclusion and exclusion criteria.
Interventions: description of intervention, comparison, duration, intensity, content of both intervention and control condition, and co‐interventions.
Outcomes: description of primary and secondary outcomes specified and collected, and the time points at which the outcomes are reported.
Notes: funding for trial, and notable conflicts of interest of trial authors.

Two review authors (JK and JIH) will independently extract outcome data from the included studies. We will note in the 'Characteristics of included studies' table if outcome data were not reported in a usable way. We will resolve disagreements by consensus or by involving a third review author (JHR). One review author (JK) will transfer data into the Review Manager 5 (RevMan 2014) file. We will double‐check that data are entered correctly by comparing the data presented in the systematic review with the study reports. A second review author (JIH) will spot‐check study characteristics for accuracy against the trial report. Should we decide to include studies published in one or more languages in which our author team is not proficient, we will arrange for a native speaker or someone sufficiently qualified in each foreign language to fill in a data extraction form for us.

Assessment of risk of bias in included studies

Risk of bias in randomised controlled trials (RCTs)

Two review authors (JK, JHR) will independently assess risk of bias for each study using the Cochrane 'Risk of bias' tool criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We will resolve any disagreements by discussion or by involving another author (JHV or JIH). We will assess the risk of bias according to the following domains.

Random sequence generation.
Allocation concealment.
Blinding of participants and personnel.
Blinding of outcome assessment.
Incomplete outcome data.
Selective outcome reporting.
Other bias.

We will grade each potential risk of bias as high, low, or unclear, and provide a quote from the study report together with a justification for our judgment in the 'Risk of bias' table. We will summarize the risk of bias judgements across different studies for each of the domains listed. We will consider blinding separately for self‐reported or administrative data of sickness absence. In case of self‐reported data we will consider the risk of bias to be high, and in case of administrative data we will consider the risk of bias due to blinding to be low. Where information on risk of bias relates to unpublished data or correspondence with a trialist, we will note this in the 'Risk of bias' table. In case of insufficient information regarding risks of bias, the authors of that study will be contacted.

Risk of bias in controlled before‐after (CBA) studies

We will use the Risk Of Bias In Non‐randomised Studies ‐ of Interventions (ROBINS‐I) tool for assessing the risk of bias in CBA studies (Sterne 2016). Our target trial against which we will assess the risk of bias would be a trial in which participants that report sick would be assigned to physician certification (or a shorter period of self‐certification) and self‐certification (or a longer period of self‐certification) at the start of sick leave. We will consider age, gender, and type of job (blue versus white collar) as potential confounders for which we expect studies to have adjusted in the design or in the analysis because these variables are related to a longer sickness absence or higher frequency of absence. We will assess waiting days or specific supervisor responsibility for sickness absence as co‐interventions that could be different between intervention and control group and have an impact on the primary outcome. We will first use the signalling questions as prescribed in the ROBINS‐I tool and then assess the risk of bias if these questions indicate a potential risk of bias.

Risk of bias in Interrupted time‐series (ITS) studies

For ITS studies, we will use the risk of bias criteria developed by the Cochrane EPOC group.

We will assess the risk of bias in ITS studies against the following criteria.

Was the intervention independent of other changes?
Was the shape of the intervention effect pre‐specified?
Was the intervention unlikely to affect data collection?
Was knowledge of the allocated interventions adequately prevented during the study?
Were incomplete outcome data adequately addressed?
Was the study free from selective outcome reporting?
Was the study free from other risks of bias?

We will judge the risk of bias of ITS studies in all of the above domains to be high, low, or unclear. When one or more domains are at high risk of bias we will consider an ITS study to be at high risk of bias.

We will consider randomisation (confounding, selection), allocation concealment, and blinded outcome assessment to be key domains. We will judge a study to have a high risk of bias overall when we judge one or more key domains to have a high risk of bias. Conversely, we will judge a study to have a low risk of bias when we judge low risk of bias for all key domains but none of the other domains at high risk of bias.

When considering treatment effects, we will take into account the risk of bias for the studies that contribute to that outcome.

Assesment of bias in conducting the systematic review

We will conduct the review according to this published protocol and report any deviations from it in the 'Differences between protocol and review' section of the systematic review.

Measures of treatment effect

For RCTs and CBA studies, we will calculate the results of each trial as point estimates, such as risk ratios (RR) for dichotomous outcomes, means and standard deviations (SD) or standardized mean differences (SMDs) for continuous outcomes, or other data types as reported by the trial authors. If only effect estimates and their 95% confidence intervals or standard errors are reported in studies we will enter these data into RevMan (RevMan 2014) using the generic inverse variance method. We will ensure that higher scores for continuous outcomes have the same meaning for the particular outcome, explain the direction to the reader and report where the directions were reversed if this was necessary. When the results cannot be plotted, we will describe them in the 'Characteristics of included studies' table, or enter the data into 'Additional tables'.

For CBA studies, we will plot the outcome measurements both at baseline and follow‐up to ensure that baseline imbalances are considered.

For ITS studies, we will extract data from original papers and re‐analyze them according to recommended methods for analysis of ITS designs for inclusion in systematic reviews and as also recommended for evaluation of law studies (Viscusi 2005). These methods utilize a segmented time‐series regression analysis to estimate the effect of an intervention while taking into account secular time trends and any auto‐correlation between individual observations. If an included ITS study uses a control group, we will use the difference in rates between the intervention and the control group as the outcome. For each study, we will fit a first‐order auto‐regressive time‐series model to the data using a modification of the parameterization of Ramsay 2003. Details of the mode specification are as follows: Y= ß0 + ß1time + ß2 (time‐p) I (time > p) + ß3 I (time > p) + E, E ˜ N (0, s2).

For time = 1,...,T, where p is the time of the start of the intervention, I (time ⋝ p) is a function which takes the value 1 if time is p or later and zero otherwise, and where the errors E are assumed to follow a first order autoregressive process (AR1). The ß‐parameters have the following interpretation: ß1 is the pre‐intervention slope. ß2 is the difference between post and pre‐intervention slopes. ß3 is the change in level at the beginning of the intervention period, meaning that it is the difference between the observed level at the first intervention time point and that predicted by the pre‐intervention time trend.

We will standardize the data of ITS studies to obtain effect‐sizes by dividing the outcome and standard error by the pre‐intervention SD as recommended by Ramsay 2003.

Thus, we will have two separate outcomes for an ITS study: the short‐term change in the level of the outcome due to the intervention, which can be interpreted as an additive effect, and the long‐term change in the trend in time or change of slope indicating an increasing effect of the intervention.

Unit of analysis issues

For studies that employ a cluster‐randomised design and that report sufficient data to be included in the meta‐analysis but that do not make an allowance for the design effect, we will calculate the design effect based on a large assumed intra‐cluster correlation of 0.10. We base this assumption of 0.10 being a realistic estimate by analogy to studies about implementation research. We will follow the methods stated in chapter 16.3.6 in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011) for the calculations.

If several active interventions have been compared with no intervention, we will divide the participants in the no intervention control group by the number of interventions, as described in the Cochrane Handbook for Systematic Reviews of Interventions for the purposes of meta‐analysis (Higgins 2011).

Dealing with missing data

We will contact investigators or study sponsors in order to verify key study characteristics and obtain missing numerical outcome data where possible (e.g. when a study is identified as abstract only). Where this is not possible, and the missing data are thought to introduce serious bias, we will explore the impact of including such studies in the overall assessment of results by a sensitivity analysis.

If numerical outcome data are missing, such as SDs or correlation coefficients, and they cannot be obtained from the authors of the original study, we will calculate them from other available statistics such as P values according to the methods described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011).

Assessment of heterogeneity

First, we will assess clinical homogeneity based on the similarity of the intervention, control condition, outcome, population, and follow‐up time. We will consider all types of participants to be similar. We will consider any introduction, abolishment, increase, or decrease in the self‐certification period to be similar. We will consider all sick leave outcomes as similar. We will consider three follow‐up time periods: up to three months, between three and six months, and more than six months, and we will analyse the included studies accordingly.

In addition, we will test for statistical heterogeneity by means of the Chi² test as implemented in the forest plots in Review Manager 5 (RevMan 2014). We will use a significance level of P < 0.10 to indicate if there is a problem with heterogeneity. In addition, we will quantify the degree of heterogeneity using the I² measure (where an I² value > 50% indicates a moderate degree of heterogeneity, and a value of > 75% a high degree of heterogeneity). When we identify ≥75% heterogeneity between studies we will refrain from pooling their results for meta‐analysis.

Assessment of reporting biases

We will reduce the effects of reporting bias by including studies and not articles. We will prevent location bias by searching multiple databases. Language bias will be prevented by not excluding any article based on language restrictions. We will check for outcome reporting bias as part of the risk of bias assessment.

Data synthesis

We will present results separately for RCTs, CBA studies and ITS studies.

We will pool data from studies judged to be clinically homogeneous with Review Manager 5 software (RevMan 2014). If possible, we will combine studies using MDs. If different outcomes do not permit pooling, then we will use SMDs. To make the SMDs more readily interpretable for clinicians, we will then recalculate the pooled SMD into an MD by multiplying the SMD by the median SD taken from the included studies using the preferred scale in question. We will pool results from studies with different study designs if the direction and the magnitude of the studies are considered similar.

To combine hazard ratios and effect sizes obtained from ITS studies we will use the generic inverse variance method as implemented in Review Manager 5 (RevMan 2014).

Given the type of interventions and the conditions under which trials will be conducted, we expect statistical heterogeneity. Therefore, a random‐effects model will be used for the meta‐analysis. If the heterogeneity between studies is low, the results will be similar to those from a fixed‐effect model. All estimates will include a 95% confidence interval (CI).

We expect that not all included studies contain economic evaluation. We will report the change in costs of short‐term sickness absence per employee and total costs of short‐term sickness absence. We will take into account variation in items included in the cost estimates (administrative costs of handling short‐term sickness absence, value of lost production, and costs of health care) and in the methods used to value these items.

Summary of findings table

We will create a 'Summary of findings' table using all primary and secondary outcomes regarding duration of short‐term sickness absence and number of short‐term absence spells for our main comparisons between self‐certification and physician certification .

We will use the five GRADE considerations (study limitations, consistency of effect, imprecision, indirectness, and publication bias) to assess the quality of a body of evidence as it relates to the studies which contribute data to the meta‐analyses for the prespecified outcomes. We will use methods and recommendations described in Chapter 8 and Chapter 12 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2017; Schünemann 2017) using GRADEpro software. We will justify all decisions to down‐ or up‐grade the quality of studies using footnotes.

We will also compile an additional GRADE table showing our decisions about the quality of evidence and their justifications.

Subgroup analysis and investigation of heterogeneity

We will compare the effects of interventions on the following three variables in subgroup analyses:

The length of increase or decrease in the self‐certification period where we will compare the effects of studies with participants that have up to seven calendar days versus more than seven calendar days of self‐certification.
The existence of so‐called waiting days, i.e. days at the beginning of sickness absence when sick pay is not payable where we will compare the effects of studies with participants that do not have waiting days versus studies with any number of waiting days.
The existence of flexible working conditions for which we will compare studies with participants that are considered not to have flexible working conditions versus those with flexible working conditions.

We will use the Chi² test to test for subgroup interactions in Review Manager 5 (RevMan 2014).

Sensitivity analysis

We will conduct sensitivity analyses to test the robustness of our meta‐analysis results by leaving out studies judged to be at a high risk of bias. We will also conduct sensitivity analyses for possible assumptions that we make for missing data or analyses during the review process.

Reaching conclusions

We will base our conclusions only on findings from the quantitative or narrative syntheses of included studies for this review. We will avoid making recommendations for practice based on anything other than the evidence. We will suggest priorities for future research and outline what the remaining uncertainties are in the area.