Endometrial injury in women attempting to conceive following sexual intercourse or intrauterine insemination: a collaborative individual participant data meta‐analysis (IPD‐MA)
Abstract
Objectives
This is a protocol for a Cochrane Review (intervention). The objectives are as follows:
To evaluate the benefits and harms of endometrial injury for reproductive outcomes in women following sexual intercourse or intrauterine insemination compared to placebo or no intervention.
Background
Description of the condition
The endometrium lines the mammalian uterus and, under the influence of oestrogen and progesterone, undergoes a cyclical pattern of development that is repeated about every 28 days. At the beginning of the menstrual cycle, the functional layer of the endometrium is shed as menstrual loss, while the basal layer remains and serves to generate a new layer of functional endometrium. Receptivity of the endometrium to an implanting embryo only occurs during a specified period of time, approximately seven to 10 days following ovulation (Viganò 2003). This is known as the 'window of implantation' and the exact timing of this window appears to vary between women (Díaz‐Gimeno 2013). Implantation of an embryo requires the sequential apposition, attachment and invasion of the blastocyst into the lining of the uterus, in order to establish a pregnancy. This process requires a functionally normal embryo, a receptive endometrium, and highly co‐ordinated signalling and synchronisation between the implanting blastocyst and the endometrium. In both natural conception and fertility treatment cycles, implantation is a key step in achieving pregnancy, and for this reason it is often referred to as the rate‐limiting step (Dekel 2010).
Repeated or recurrent implantation failure describes the clinical situation in which a woman fails to achieve pregnancy after the transfer of multiple good‐quality embryos, though a definitive definition of this condition remains controversial (Coughlan 2014; Li 2014; Polanski 2014; Vlachadis 2014). Owing to the occurrence of recurrent implantation failure even when high‐quality embryos are replaced, endometrial receptivity is believed to play a central role in this condition. Poor endometrial receptivity has also been implicated in subfertile conditions such as unexplained infertility, endometriosis, polycystic ovarian syndrome, autoimmune disorders, hydrosalpinx and pathological microbiota (Altmäe 2010; Garzia 2004; Jana 2013; Jokimaa 2002; Moreno 2016; Nacak 2018; Savaris 2007).
Description of the intervention
Endometrial injury (also known as endometrial scratching, irritation, disruption, disturbance, biopsy or sampling) is currently being suggested as a potential treatment to improve endometrial receptivity and thereby pregnancy rates in women undergoing assisted reproductive technology. Endometrial injury is defined as intentional damage to the endometrium with the objective of improving reproductive outcomes (Nastri 2012). The most common procedure used to administer endometrial injury is an endometrial biopsy, usually performed with a soft plastic endometrial biopsy catheter such as a Pipelle de Cornier (Laboratoires CCD, France). Other devices may be considered to cause a more intense disturbance to the endometrium, such as a hysteroscope or a Novak curette, whilst others may cause a lesser disturbance, such as a Tao brush (Abdelhamid 2013; Rigos 2021; Siristatidis 2017).
How the intervention might work
Descriptions of the effect of endometrial trauma were initially reported more than a century ago, when researchers experimenting with rodents observed that uterine incisions induced decasualisation, a process of transforming uterine endometrium to decidua which normally only occurs in the period in which rodents conceive. In women, decasualisation occurs monthly in preparation for implantation under the influence of progesterone (Loeb 1907). The observation that in women, routine luteal phase endometrial biopsy did not preclude pregnancy in the same cycle led North American investigators to hypothesise a therapeutic effect; suggesting endometrial trauma in close proximity to the time of implantation (same cycle) may stimulate a better decidual reaction in terms of promoting greater proliferative changes in the endometrium, and hence preserving pregnancies that may otherwise have been lost (Karow 1971).
Further potential mechanisms of following endometrial injury have also been proposed, outlining a complex series of biological responses leading to improved pregnancy rates and ultimately concluding that no specific pathway is solely responsible for this outcome (Siristatidis 2014). Such mechanisms include:
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the 'mechanical hypothesis', which proposes that exogenous injury transforms the endometrium into a receptive state and enhances its synchronicity with the transferred embryo;
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the 'inflammation hypothesis' per se, which suggests that the inflammatory reaction caused by endometrial injury increases receptivity through a cascade of macrophages, dendritic cells, cytokines and chemokines;
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the hypothesis concerning the events accompanying wound healing, which describes how the process of endometrial restoration and tissue regeneration following injury may promote a more favourable environment for implantation;
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the immune system cell recruitment, which describes how recruitment of immune cells to the area of endometrial injury may facilitate embryo implantation;
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the 'gene expression theory'; which proposes how endometrial injury may regulate the expression of genes related to endometrial receptivity;
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the 'neoangiogenesis theory', which describes how endometrial injury may provide an enhanced angiogenic environment important for trophoblast invasion and embryo retention;
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protein involvement, due to the variety of proteins known to co‐act in the differentiation of the endometrium after injury;
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the treatment of certain female genital tract infections, due to the potential association with type 2 immunity and gene expression;
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the potential differentiation of gene‐associated oxidative stress (Siristatidis 2014).
Why it is important to do this review
The utility of endometrial injury in women undergoing assisted reproductive technologies has been investigated several trials with variable conclusions (Baum 2012; Guven 2014; Karim Zadeh Meybodi 2008; Shohayeb 2012). The first Cochrane Review on this suggested that endometrial injury was associated with an improvement in live birth rate in women with more than two previous embryo transfers (Nastri 2015). In the update, the primary analysis was restricted to studies at low risk of bias, and found the effect of endometrial injury on live birth was unclear (odds ratio (OR) 1.12, 95% confidence interval (CI) 0.98 to 1.28; 8 studies, 4402 participants; I2 = 15%; moderate‐certainty evidence). Outside the in vitro fertilisation setting, several trials in women attempting to conceive via sexual intercourse or intrauterine insemination investigated the potential effect of endometrial injury. Some trials have shown a beneficial effect of endometrial injury (Goel 2017; Gupta 2018; Maged 2016; Parsanezhad 2013; Soliman Badeea 2017), whilst some could not detect a significant improvement (Gibreel 2019; Zarei 2014). One recent Cochrane Review on this topic concluded that it is still unknown whether endometrial injury improves the probability of live birth or ongoing pregnancy (Bui 2022), whilst an earlier review found a strong beneficial effect but with low‐certainty evidence (Lensen 2016).
In recent times, the issue of data integrity in randomised controlled trials (RCTs) has become a cause for concern – especially when treatment effects may be inaccurately reported and lead to patient harm (Bordewijk 2020a; Liu 2023). When RCTs are summarised into systematic reviews and meta‐analyses there is a need to ensure that the evidence base is trustworthy. Previous analysis of RCTs evaluating endometrial injury found that most had methodological issues which may have biased their overall results (Li 2019). Given these known issues, collecting individual participant data (IPD) for these RCTs is an important step to ensure the validity and accuracy of their results (Bordewijk 2020b). In view of the above, an IPD Cochrane Review is needed to enable making conclusions based on the best evidence (Tierney 2023).
Objectives
To evaluate the benefits and harms of endometrial injury for reproductive outcomes in women following sexual intercourse or intrauterine insemination compared to placebo or no intervention.
Methods
Criteria for considering studies for this review
Types of studies
In this systematic review with individual participant data meta‐analysis (IPD‐MA), we will only include RCTs. We will exclude pseudo‐randomised trials and other study designs. There will be no restrictions regarding the minimal time of follow‐up or number of included participants. We will include studies reported as full text, those published as abstract only and unpublished data, such as recent unpublished trials or older trials that were unable to be published due to internal issues.
Types of participants
Women with infertility or couples who are trying to get pregnant, either with sexual intercourse or intrauterine insemination, with or without ovulation induction. We will exclude women or couples undergoing assisted reproductive technology (e.g. in vitro fertilisation) as they are the topic of another Cochrane Review (Lensen 2021).
Types of interventions
Endometrial injury compared to placebo or no intervention with the objective of improving the reproductive outcome of women desiring pregnancy. Endometrial injury is defined as intentional disturbance to the endometrium with the purpose of improving endometrial receptivity. Endometrial injury may be performed by endometrial biopsy catheter (e.g. Pipelle) or curette. Intentional endometrial injury via hysteroscopy will also be included, but not hysteroscopy without this as a primary purpose. Other procedures that are also likely to cause some endometrial disruption, but which are not intentional injury (e.g. hysterosalpingogram, saline‐infusion ultrasound, etc.), or procedures of which the extent of the endometrial disruption is not visible (e.g. saline‐infusion) will not be included.
Types of outcome measures
Primary outcomes
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Live birth or ongoing pregnancy from the cycle after randomisation per woman randomised (efficacy outcome). Live births are defined as the delivery of a live fetus after 20 completed weeks of gestation. Multiple births will be counted as one live birth event. Ongoing pregnancy is defined as a positive fetal heartbeat on ultrasound from a gestational age of 12 weeks onwards
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Miscarriage from the cycle after randomisation (safety outcome). Miscarriage is defined as a loss of clinical pregnancy before 20 weeks of gestation
Secondary outcomes
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Cumulative live birth rate, defined as the proportion of pregnancies leading to a live birth within the time horizon as set by the study
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Clinical pregnancy from the cycle after randomisation; clinical pregnancy is defined as the presence of a gestational sac on ultrasound at a gestational age of six to seven weeks
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Pregnancy loss from the cycle after randomisation; including:
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ectopic pregnancy,
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miscarriage,
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stillbirth,
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termination of pregnancy
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Multiple pregnancy from the cycle after randomisation
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Gestational age at delivery
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Pain during the procedure and adverse events (e.g. infection, bleeding)
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Implantation‐related obstetric outcomes, including hypertensive disorders of pregnancy, placental adhesive disorders (e.g. placenta accreta) and placental abruption
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Neonatal outcomes, including birthweight, neonatal mortality and major congenital abnormalities (Duffy 2020)
Search methods for identification of studies
We will search for RCTs that describe endometrial injury in women attempting to conceive following sexual intercourse or intrauterine insemination, using a search strategy developed in consultation with the Information Specialist for the Cochrane Gynaecology and Fertility Group. We will use both indexed and free‐text terms and will not apply any language or date restrictions.
Electronic searches
We will search the following databases.
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The Cochrane Gynaecology and Fertility Group's (CGF) specialised register of controlled trials, to search from inception to present, PROCITE platform (Appendix 1)
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CENTRAL, via the Cochrane Register of Studies Online (CRSO); to search from inception to present, Web platform (Appendix 2)
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MEDLINE, to search from 1947 to present, Ovid platform (Appendix 3)
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Embase, to search from 1980 to present, Ovid platform (Appendix 4)
The MEDLINE search was limited by the Cochrane highly sensitive search strategy filter for identifying randomised trials, which appears in the Cochrane Handbook of Systematic Reviews of Interventions (Section 6.4.11; Lefebvre 2011). We combined the Embase searches with trial filters developed by the Scottish Intercollegiate Guidelines Network (SIGN) (www.sign.ac.uk/what-we-do/methodology/search-filters/).
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We will also contact potential trialists to establish expressions of interest regarding collaboration. We will seek further trial details, protocols, and case report forms to establish eligibility of potential trials. We will update the search before the end of the project to avoid missing recently published studies.
Searching other resources
We will handsearch reference lists of relevant articles retrieved by the search. Where possible or relevant, we will contact experts in the field (e.g. authors or investigation groups of already included studies) for information on additional trials, including unpublished or in progress trials.
We will also search the international trial registers: the ClinicalTrials database, a service of the US National Institutes of Health (clinicaltrials.gov/ct2/home) and the World Health Organization International Trials Registry Platform search portal (www.who.int/trialsearch/Default.aspx).
Data collection and analysis
Selection of studies
Two review authors (SL and MP) will independently screen the titles and abstracts of all articles retrieved from the searches according to the review inclusion criteria. We will exclude any studies that are clearly irrelevant. We will retrieve full‐text versions of the remaining potentially eligible studies. Two review authors (SL and MP) will independently screen the full texts. We will exclude articles that do not meet the review inclusion criteria giving reasons in the 'Characteristics of excluded studies' table. Due to the specific interventions and comparators under investigation, blinding of the participant and the treating physician is technically or ethically impossible (or both) and is therefore not considered an inclusion or exclusion criterion. In instances where the eligibility of the study is unclear, we may contact the study authors for clarification. We will resolve disagreements between the two review authors by discussion with a third review author (CS). We will translate studies in any language other than those known by the review authors with the help of Cochrane and assess them for eligibility. We will include studies that do not report any outcome measures relevant to this review until we have contacted the study authors to confirm that these outcomes were not measured.
Data extraction and management
An initial project management and advisory group will be established and be responsible for contacting and liaising with study authors, data collection, checking and analyses, interpretation of findings, and preparing manuscripts for publication. A further collaborative group will then be formed from the management group and authors of included studies. Members of the collaborative group will have the opportunity to make edits and comments on the draft manuscript before being finalised (Tierney 2023).
We will contact corresponding or primary authors of the included studies by email to invite them to collaborate and share their raw data. If there is no response, we will contact co‐authors via email. If also unresponsive, we will contact institutions associated with the authors including hospitals and universities, co‐authors on more recent publications with the author of interest, colleagues from our network in the same country as the author of interest and finally the journal the eligible RCT was published in. In the case of unpublished data, we will attempt to contact known investigators from details in any potential trial registration or via institutional links.
We will collect the following data: study characteristics (e.g. number of recruitment centres, number of participants randomised, study registration details), baseline characteristics and outcome data (Appendix 5). Where studies have multiple publications, we will collate the multiple reports of the same study so that each study, rather than each report, is the unit of interest in the review, and such studies have a single study ID with multiple references. For analysis purposes, we will only use the most relevant data for this review. We will correspond with study investigators for further data on methods or results as required.
Quality control
We will rigorously check all data for discrepancies and clarify all discrepancies with the author(s) of the dataset. This will include assessing for missing or excluded data, checking for errors, checking for the presence of randomisation and checking internal consistency. We will also replicate the baseline outcomes and results from the published trial with the trial's raw data. We will check the completeness and integrity of incoming data according to suggestions in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2022a), including randomisation sequence, omissions or duplicates in the sequence of participant identifiers, missing, invalid, out of range or inconsistent items. Also, we will check the data supplied against any relevant study publications or results repositories.
Assessment of risk of bias in included studies
Two review authors (SL and MP) will independently assess study quality and risk of bias. A third review author will check studies in which there is any disagreement about study quality. We will assess bias using the Cochrane RoB 2 tool, which contains specific items that assess five domains where bias may arise (e.g. from the randomisation process, deviations from intended interventions, missing outcome data, measurement of the outcome and selection of the reported results) (Sterne 2019; Higgins 2022b). Regarding the comparison of endometrial injury with placebo or no intervention, we will explore bias for the intention‐to‐treat effect (i.e. the effect of assignment to each intervention) for all the investigated outcomes (see Types of outcome measures).
We will judge each domain of bias as 'low', 'high' or 'some concerns' after answering the signalling questions, supporting the answers with proper justification and quotations from the trial's text or registered protocol (or both), and verifying the judgements proposed by the tool's algorithms. These five domain‐level judgements will provide the basis for the overall assessment. We will reach an overall risk‐of‐bias judgement for each outcome of each study after verifying the algorithm's suggestions. We will judge trials at high risk of bias if they are subject to high risk of bias in at least one domain or to some concerns in multiple domains for the result, unless we can justify a different judgement; low risk of bias if they are at low risk of bias for all domains; and to have some concerns of risk of bias if we have some concerns for at least one domain for this result. In cases where study quality is unclear from trial protocols/publications, or if any questions arise, we will contact the principal investigators for clarification. We will implement the Excel tool for RoB 2 to efficiently store and present our judgements and their justifications (available from www.riskofbias.info/). This will be part of a separate document that we will make available with the review as an online supplemental file.
Measures of treatment effect
For dichotomous data (e.g. live birth), we will use the numbers of events in the control and intervention groups of each study to calculate ORs. For continuous data (e.g. pain), if studies report the same outcomes using the same scales, we will calculate mean differences (MDs) between treatment groups. If studies report similar outcomes using different scales, we will calculate the standardised mean difference (SMD). We will reverse the direction of effect of individual studies, if required, to ensure consistency across trials. We will present 95% CIs for all outcomes. For studies where IPD is requested but not shared, we will perform aggregate data meta‐analysis and compare results on primary outcomes to those where IPD is shared.
Unit of analysis issues
The primary analysis for the primary outcomes will be per woman randomised. For secondary outcomes, we will analyse data based on the randomised groups. We will briefly summarise data that do not allow valid analysis in an additional table and will not perform meta‐analysis. We will include only the first‐phase data from cross‐over trials.
Dealing with missing data
We will analyse the data on an intention‐to‐treat basis as far as possible and attempt to obtain missing data from the study investigators. Where these are unobtainable, we will impute individual values as described below.
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We will assume live births have not occurred in participants without a reported outcome.
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When a study compares endometrial injury with no intervention and reports pain only for the intervention arm, we will assume pain to be zero in the control arm.
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When a study reports both live birth and clinical pregnancy, but not miscarriage, we will determine the number of miscarriages as the difference between clinical pregnancy and live birth, as the prevalence of stillbirth is less than 1% of clinical pregnancies (Joseph 2013).
For other outcomes, we will analyse only the available data. Any imputation undertaken will be subject to sensitivity analysis.
Assessment of heterogeneity
We will consider whether the clinical and methodological characteristics of the included studies are sufficiently similar for meta‐analysis to provide a clinically meaningful summary. We will assess statistical heterogeneity using the I2 statistic, and will consider an I2 value greater than 50% to indicate substantial heterogeneity (Higgins 2022a). We will investigate causes of any observed heterogeneity with prespecified subgroup analyses.
Assessment of reporting biases
Assessment of data unavailability bias
In view of the possibility that not all studies provide participant‐level data, we will perform an aggregate data meta‐analysis pooling RCTs that did not provide data for the primary outcome. We will compare effect estimate of RCTs that did not contribute data to the main analysis with participant‐level data and calculate ratios of ORs.
Data synthesis
We will develop coding sheets, a database structure and variables, and a detailed analysis plan agreed on by all review authors. We will prepare data request documents; transfer mechanisms; and procedures for central collection, checking and re‐coding of trial data. Subsequently, we will prepare a process of verification ('sign‐off') of finalised data which each of the trialists will follow. This will form the basis of the analysis. We will pool data and use them in a coded form. The key to link coded data to individual participants will remain in the possession of each original trialist.
We will assess data quality by comparison of the shared data with the numbers published by the principal investigator. In case of discrepancies, we will contact the principal investigator and make corrections as necessary. We will include only data from completed trials, and exclude data from interim analyses. We will determine the exact method of data analysis based on the characteristics of the data. We will develop a detailed analysis plan, which will be agreed upon by all collaborators before starting data analysis. We will aim to use the two‐stage approach as the first choice to synthesise the IPD. In the first stage, we will compare outcomes following endometrial injury to no intervention or placebo adjusting for confounders. In the second stage, we will combine generated relative estimates using random‐effects models. The models will have a stratified intercept and a random treatment effect. We will perform the one‐stage approach as a sensitivity analysis. However, in the case that there are over 25% of trials that are small (i.e. fewer than 30 participants) or there are zero event counts for any outcome comparison, the one‐stage approach will be the first choice.
We will restrict our primary analysis to studies judged at low risk of bias based on their RoB 2 assessments for each outcome. We will extract aggregate data from publications for trials that did not share IPD, and combine these with individual risk estimates calculated for each trial supplying IPD in two‐stage meta‐analyses.
Subgroup analysis and investigation of heterogeneity
We will use an effect modifier approach to estimate the interactions of clinically important subgroups. We will limit analyses to the primary outcomes only. We will estimate interaction terms of each study and pool them in a meta‐analysis of interactions. Conclusions on interactions will be based on the within‐trial level. We will study the following hypothesised participant‐level modifiers of treatment for the primary effectiveness outcome.
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Female age
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Body mass index
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Duration of infertility
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Diagnosis (i.e. type of infertility)
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Type of endometrial injury (i.e. undergoing endometrial injury with different injury techniques/tools)
Sensitivity analysis
We will conduct sensitivity analyses based on methodological quality by repeating the IPD analysis using all available data (including studies at high risk of bias). We will limit the sensitivity analyses to the primary outcomes. Where studies have not provided IPD, we will combine their aggregate data with the available IPD to assess the robustness of including or excluding these studies. This analysis will be conducted with fixed‐effect modelling and risk ratios.
Summary of findings and assessment of the certainty of the evidence
We will create a summary of findings table using GRADEpro GDT software and the Cochrane Handbook for Systematic Reviews of Interventions (GRADEpro GDT; Higgins 2022a). This table will evaluate the overall certainty of the body of evidence for the primary and some secondary outcomes for the review comparison of endometrial injury compared to placebo or no intervention in addition to appropriate subgroup analyses. In addition to the primary outcomes of live birth or ongoing pregnancy and miscarriage, we will include the secondary outcomes of cumulative live birth rate, pregnancy loss, multiple pregnancy and gestational age at delivery.
Two review authors (SL and MP) will independently use the GRADE criteria to assess the levels of evidence as high, moderate, low or very low based on the five considerations (overall risk of bias, consistency of effect, imprecision, indirectness and publication bias) for potential downgrading and three considerations (large effects, dose response, and opposing plausible confounding) for potential upgrading. We will resolve disagreements through discussion with another review author (CS). Regarding the overall risk of bias criterion, we will use the overall RoB 2 judgement for the result of each outcome to feed into the GRADE assessment. We will justify, document and incorporate judgements about evidence certainty into reporting of results for each outcome.
