We followed the PRISMA (Preferred Reporting Items for Systematic Reviews and Meta-Analyses) guidelines (see Multimedia Appendix 1) [16]. The protocol was registered a priori with PROSPERO (International Prospective Register of Systematic Reviews; registration number CRD42023404402) [17]. We searched MEDLINE, Web of Science, Embase, the Cochrane Library from inception to October 15, 2025, using MeSH (Medical Subject Headings) and free-text terms, with a validated randomized controlled trial (RCT) filter. A snowball search was conducted to identify references cited by and citations of eligible studies identified through the database searches. The full search strategies for all databases are available in Multimedia Appendix 2.

We included single and cluster RCTs comparing TECC with routine in-person CC among women and girls of any age or setting. Only full, published, English-language reports were eligible; abstracts and study protocols were excluded. Intervention eligibility required meeting 3 core domains: telehealth delivery modality, interactivity, and tailoring. Telehealth delivery modalities included phone or video calls, voice or SMS text messaging, mobile apps, and websites. Interactivity implied bidirectional communication to some degree, excluding, for example, unidirectional information delivery or reminders. Tailoring meant that interventions were individualized to users’ input, generating adapted output based on at least one of the following domains: contraceptive preferences, reproductive goals, medical history, or method-specific information on benefits, side effects, and effectiveness. Interventions could be delivered in real time or asynchronously, with or without human involvement. Interventions could be delivered before, during, or after a clinical visit and could complement or substitute for in-person clinical care. We categorized models in which TECC was delivered as an adjunct to in-person care as hybrid models. Hybrid models were eligible if the telehealth component independently met the tailoring and interactivity criteria. Shared decision-making tools used in provider-led consultations were excluded. Our comparator was any form of routine CC delivered in person as verbal or written information, provided individually or in groups. Studies using telehealth as a comparator were excluded. The rationale for excluding other digital interventions as comparators was to assess the effect of the telehealth component on CC. An overview of the concepts in our definition of TECC is provided in Multimedia Appendix 3.

Our primary outcome was the use of any effective contraceptive method (ECM) up to 6 months after the intervention. We distinguished use from continuation or adherence to a specific method. ECM was defined as long-acting reversible contraception (LARC), including the progestin implant and hormonal or copper intrauterine devices; combined oral contraceptives; progestin-only pills; progestin injections; the contraceptive patch; the contraceptive ring; and sterilization—methods with typical-use failure rates of less than 10% per year [18]. Additional outcomes were (1) ECM use at 6-12 months; (2) LARC use at less than 6 months; (3) LARC use at 6-12 months; (4) choice of ECM at the time of counseling; (5) choice of LARC at the time of counseling; (6) satisfaction with counseling at less than 6 months; and (7) method switching.

“Use” was assessed based on self-reported or recorded use in follow-up surveys or clinical records. Where multiple time points were reported, we prioritized the time point that enabled comparison across the greatest number of studies or, secondarily, the latest time point within the specified range. “Choice” was defined as documented intention to use a specific method immediately after counseling. We defined “switching” as a documented change from no method or a less effective method to a more effective ECM. “Satisfaction” included any reported measure of satisfaction with counseling up to 6 months after the intervention.

After deduplication of the final search results, we imported records into Rayyan for screening. Three reviewers (MW, AK, and ME) independently screened titles and abstracts. We unblinded the selection process after the initial screening and resolved discrepancies through discussion. We retrieved and assessed full-text articles against the inclusion criteria, and disagreements were resolved through discussion until consensus was reached. Records excluded at the full-text review stage and the reasons for exclusion are provided in Multimedia Appendix 4.

Data on publication year, study design, setting, participant characteristics, intervention, comparator, and raw data for each outcome were extracted by one reviewer (MW) from full-text articles, supported by GPT-4o (OpenAI, May 2024) as a preliminary extraction tool for nonoutcome study characteristics (population, setting, intervention, and comparator descriptions). All AI-assisted outputs were reviewed and corrected against the source articles by MW and then verified by ME. Studies in which data relevant to our outcomes were grouped in a way that did not permit the extraction of stratified data, or in which outcome data were missing, were excluded from the analysis.

Risk of bias (RoB) was assessed independently by reviewers MW and ME for each outcome using the Cochrane RoB 2 tools for RCTs and cluster RCTs, respectively [19]. Five domains were evaluated, including (1) bias arising from the randomization process, (2) bias due to deviations from intended interventions, (3) bias due to missing outcome data, (4) bias in outcome measurement, and (5) bias in the selection of the reported result. Discrepancies were resolved through discussion until consensus was reached.

Assessment of the overall certainty of evidence was performed using the GRADE (Grading of Recommendations Assessment, Development, and Evaluation) approach for each outcome. GRADE ratings were independently assessed by MW and ME; discrepancies were resolved through discussion until consensus was reached [20]. As we included only RCTs, the certainty of evidence started as high and was downgraded based on RoB, inconsistency, imprecision, indirectness, and publication bias. Statistical heterogeneity was quantified using the I² statistic in accordance with the Cochrane Handbook for Systematic Reviews of Interventions, with 50%-90% potentially representing substantial heterogeneity and 75%-100% representing considerable heterogeneity. Our interpretation was informed by the magnitude and direction of effects, the number and size of contributing studies, and the plausibility of clinical or methodological diversity. We considered downgrading for inconsistency if I² exceeded 50%. Imprecision was assessed using the optimal information size (OIS) criterion, in accordance with GRADE guidance for systematic reviews [21]. For each outcome eligible for meta-analysis, OIS was determined using the reference values reported by Guyatt et al [21], applying the observed pooled control event rate and the GRADE-recommended default relative risk (RR) reduction of 25%, with α=.05 and power of 80%. Certainty of evidence was downgraded by 1 level for imprecision when the total sample size contributing to the pooled estimate fell below the corresponding OIS threshold. Where the OIS threshold was met but the 95% CI of the pooled effect crossed or narrowly excluded the line of no effect, we additionally considered whether the CI excluded an appreciable effect, using the GRADE default RR reduction threshold of 25% for appreciable benefit or harm. For outcomes not eligible for meta-analysis (LARC use at 6-12 months, choice of LARC, and satisfaction with counseling), imprecision was judged by comparing the combined sample size across contributing studies with the OIS reference and by inspecting the width of individual study CIs in relation to the line of no effect. Imprecision judgments for each outcome are documented in the footnotes to Table 3.

We grouped studies for each synthesis according to outcome and follow-up time point. Studies reporting data in a comparable format were included in random-effects meta-analyses when at least 2 comparable studies were available. We calculated RRs with 95% CIs for all outcomes based on available data from intention-to-treat study groups, deriving them from raw data or alternative effect measures, and presented pooled results as forest plots. Heterogeneity was assessed using the I² statistic and interpreted in relation to the direction and consistency of effects across studies. For outcomes for which data quality or heterogeneity did not support meta-analysis, we reported results descriptively and interpreted them exploratorily. Prespecified exploratory subgroup analyses were performed by country income level (low- and middle-income countries [LMICs] versus high-income countries [HICs]). One included cluster RCT (Dehlendorf et al [22]) was randomized at the provider level (28 providers; mean cluster size of ≈27). Raw event counts per study arm were extracted from the published article. As the reported provider-level intracluster correlation coefficient was approximately 0, the corresponding design effect was ≈1.0, and no design-effect adjustment was applied. Sensitivity analyses examined the effect of publication year (before vs after 2015), which stratifies the approximately 20-year period during which telemedicine has been used for reproductive health, and low versus moderate or high RoB. Where meta-analysis was not feasible, we summarized findings narratively using incidence ranges. We conducted analyses using SPSS (version 30; IBM Corp) and Review Manager (RevMan 5, desktop version).

This review used only publicly available data and required no ethical approval. There was no funding source for this study. GPT-4o (OpenAI, May 2024) was used as a preliminary tool for data extraction of setting, population, intervention, and comparator characteristics from full-text articles; for the generation of a conceptual figure; and to support language editing. All AI-assisted data extraction outputs were verified and corrected against the source articles by reviewer MW and subsequently by ME. All analyses, interpretations, and conclusions were independently conducted by the authors. Outcomes related to potential harms were not prespecified, which we acknowledge as a limitation of the protocol.

The initial protocol was amended in the following ways before data extraction: outcomes were reorganized to specify a single primary outcome; the population eligibility criterion was clarified to restrict inclusion to women and girls of any age (including adolescents); men and couples were excluded; and subgroup and sensitivity analyses were added. The revised protocol also clarified our a priori intent to restrict the search to English-language publications.

Patients or members of the public were not involved in the design, conduct, reporting, or dissemination of this systematic review.

From 8897 records screened, 8 individual RCTs and 1 cluster RCT met the inclusion criteria, involving 5353 participants from 5 HICs and 4 middle-income countries. The PRISMA flowchart illustrates the selection process (Figure 1), and Table 1 presents the study characteristics and sample sizes. Included studies were conducted in antenatal care [23,24], postabortion care [25-27], and routine contraceptive services [22,28-30]. Sample sizes ranged from 86 to 1475 participants.

All interventions fulfilled the 3 core components of our definition of TECC—telehealth delivery modality, interactivity, and tailoring—but the degree of interactivity and tailoring varied. Eight were hybrid models, delivered in addition to, before, during, or after an in-person clinical visit. Only one study [27] tested a standalone model that substituted for in-person care using telephone calls, but recruitment was terminated after only 125 of the 1222 (10.23%) planned enrollment due to changes in the comparator condition in response to the COVID-19 pandemic. The TECC modality and degree of interactivity ranged from potentially interactive voice [25,26] or SMS text messaging [23] with interaction on demand; asynchronous, self-guided computer- [28,29] or tablet-based modules [22,30]; to video or telephone calls delivered in real time [24,27]. Provider involvement in the TECC component, therefore, ranged from minimal to high. Tailoring also varied, ranging from SMS text or voice messages tailored to an already chosen method [23,25,26] to decision aids limited to life preferences and excluding medical criteria [29], comprehensive tailored decision aids [22,28,30], and real-time individualized assessments [24,27].

Comparators were standard in-person CC, with or without printed materials. In 1 trial [29], controls were offered delayed access to TECC after study completion. Table 2 outlines the intervention and comparator characteristics. Studies grouped by outcome and RoB assessment are presented in Figure 2 (also see [22-30]). Multimedia Appendix 5 details study outcomes and findings, and Multimedia Appendix 6 details how each intervention met the tailoring and interactivity criteria, as well as additional intervention characteristics that may have modified effects. GRADE-assessed certainty of evidence ranged from low to very low across outcomes. The GRADE assessment is presented in the summary of findings (Table 3), and a breakdown of each GRADE assessment is provided in Multimedia Appendix 7; 7 hybrid models and 1 standalone model contributed outcome data to the meta-analyses. One hybrid model contributed data for the outcome of satisfaction, which was reported descriptively [24].

RoB assessments for each outcome are presented in Figure 2. Four studies [23,25,26,30] had low RoB across all domains and outcomes. The most frequent concerns related to the randomization process, including sequential allocation to control and intervention arms, imbalanced distribution of study groups across study sites, changes to the randomization procedure [28], and small but potentially meaningful baseline imbalances [22,24,27,28].

Stephenson et al [29] had moderate RoB in domain 5 (selection of the reported result) due to post hoc changes in study outcomes when the trial expanded from a feasibility study to an effectiveness trial without a prespecified analysis plan. We therefore judged this outcome to have moderate RoB. We classified the studies by Saglam Aksut and Inam [24] and Dehlendorf et al [22] as having high RoB for satisfaction with counseling outcomes because outcome measurement was conducted by study staff, creating a risk of social desirability bias.

Four studies (n=2180) reported on our primary outcome, use of ECM less than 6 months after the intervention. The meta-analysis indicated a small positive but nonsignificant (P=.21) effect of TECC compared with standard care (SC; RR 1.10; 95% CI 0.95-1.29; I²=77%; Figure 3; see also [22,23,25,26]). The certainty of evidence was low, downgraded for inconsistency and imprecision (Table 3).

Four studies (n=2043) reported data on ECM use at 6-12 months after the intervention. The meta-analysis showed a small positive effect that reached statistical significance (P=.04), although the CI only narrowly excluded the null (RR 1.07; 95% CI 1.002-1.130; I²=4%; Figure 4; see also [22,23,26,29]). The certainty of evidence was low, downgraded for RoB and imprecision (Table 3).

Our subgroup and sensitivity analyses assessed whether the effect of TECC on ECM choice and use varied by country income level, RoB, and publication period. Two subgroups overlapped: studies evaluating ECM use in LMICs also had low RoB. These analyses included a small number of studies, and the results should be interpreted with caution. Pooled results for ECM use at 6-12 months among studies conducted in LMICs with low RoB (n=580) showed that TECC significantly (P=.02) increased use (RR 1.20; 95% CI 1.03-1.30; I²=0%; Figure 5; see also [23,26]). The certainty of evidence was low, downgraded for serious imprecision (Table 3). We found no evidence of an effect on ECM choice or ECM use at 6-12 months in studies from HICs with moderate-to-high RoB, or on ECM use less than 6 months in LMICs. Comparisons by publication period (pre- versus post-2015) showed no differences in ECM choice or use. Subgroup analyses based on geographic region and ECM use less than 6 months in HICs were not possible because of the small number of studies.

Two studies (n=1203) reported on LARC use at 0-6 months. Both studies were conducted in low-income settings in a postabortion context and used interactive voice messaging for TECC. However, statistical heterogeneity was high (I²=96%), and pooled estimation was not considered appropriate. Reiss et al [25] reported no significant difference between groups (RR 0.80; 95% CI 0.56-1.14), whereas Smith et al [26] found an effect in favor of the telehealth intervention (RR 3.35; 95% CI 2.07-5.40). The certainty of evidence was very low, downgraded for moderate RoB and serious imprecision (Table 3).

Two studies (n=1042) reported LARC use at 6-12 months (Smith et al [26] and Stephenson et al [29]). Statistical heterogeneity was very high (I²=87%) across 2 studies with different populations (postabortion care in Cambodia vs routine sexual health clinic attendees in the United Kingdom) and delivery modalities. Given these differences, pooled estimation was not considered appropriate. Smith et al [26] reported higher LARC use in the intervention group at 6 months compared with in-person care (RR 2.08; 95% CI 1.27-3.42), whereas Stephenson et al [29] reported no difference at 12 months (RR 0.98; 95% CI 0.79-1.22). The certainty of evidence was very low, downgraded for RoB, inconsistency, and serious imprecision (Table 3).

Four studies (n=2599) assessed the choice of ECM immediately after the intervention. The meta-analysis showed no clear evidence (P=.21) of an effect of TECC compared with SC (RR 1.07; 95% CI 0.96-1.18; I²=59%; Figure 6; see also [22,27,28,30]). The certainty of evidence was very low, downgraded for RoB, inconsistency, and imprecision (Table 3).

Two small studies (n=366) assessed the choice of LARC: 1 was conducted in a postabortion setting in the United Kingdom and was terminated early, and the other was conducted in general gynecologic clinics in the United States. Pooled analysis was not considered appropriate because the total sample size did not meet the OIS threshold and clinical heterogeneity was high across study populations, interventions, and contexts. Neither study showed increased choice of LARC at the time of counseling after TECC compared with in-person care: Reynolds-Wright et al [27] (RR 0.77; 95% CI 0.30-1.93) and Madden et al [30] (RR 1.04; 95% CI 0.74-1.47). The certainty of evidence was very low, downgraded for RoB and imprecision (Table 3).

Subgroup and sensitivity analyses examining whether the effect of TECC on ECM choice varied by publication period (P=.52) or RoB (P=.55) showed no significant effects. Subgroup analyses of LARC choice could not be performed because of the small number of studies.

Two studies (n=749) reported on satisfaction with counseling (Saglam Aksut and Inam [24] and Dehlendorf et al [22]). Madden et al [30] noted no difference in satisfaction but did not report data suitable for extraction. Meta-analysis was not possible because of differences in outcome measurement and reporting. Saglam Aksut and Inam [24] reported significantly higher satisfaction scores for TECC compared with SC (mean 174.86, SD 7.71 vs mean 154.63, SD 26.54; P<.001). However, both groups scored well above the predefined threshold for high satisfaction (142 on the 185-point scale used). Dehlendorf et al [22] found no difference in overall satisfaction between groups (odds ratio [OR] 1.11; 95% CI 0.74-1.67), but a higher proportion of TECC users assigned the highest quality ratings (266/404, 65.8% vs 198/345, 57.4%; OR 1.45; 95% CI 1.03-2.05), suggesting that TECC improved perceived counseling quality. The certainty of evidence was very low, downgraded for high RoB, inconsistency, and imprecision (Table 3).

One study reported on method switching following TECC, but did not provide sufficient detail on the methods switched from and to; therefore, the outcome could not be analyzed [29].

Only 2 studies explicitly evaluated potential harms as prespecified outcomes. Reiss et al [25] found a statistically significant increase in self-reported physical intimate partner violence (IPV) in the intervention arm compared with the control arm after menstrual regulation (11% vs 7%; adjusted OR 1.97; 95% CI 1.12-3.46). Menstrual regulation is a pragmatic term used for abortion care in Bangladesh, where abortion is illegal. This finding was detectable only when closed questions naming specific acts of violence were used; the open adverse event question (Did anything happen to you as a result of being in this study?) yielded no reports of violence in either arm. Smith et al [26] found no evidence of adverse outcomes, including domestic abuse or road traffic accidents. Other studies did not prespecify or systematically report unintended consequences, representing a gap in the evidence.

We observed 2 forms of heterogeneity. Clinical heterogeneity was considerable, arising from differences in intervention design, including timing, delivery modality, provider involvement, and study setting. Studies were conducted across a range of care settings, including antenatal, postpartum, abortion, family planning, and general gynecologic clinics. Given the small number of studies available for each outcome, stratified analyses by clinical setting were not feasible. Although all interventions met our inclusion criteria for tailoring and interactivity, the extent of user engagement and integration with clinical care varied. Second, statistical heterogeneity was considerable for some outcomes (I²>85%), as reflected by the wide CIs around pooled effect estimates. The scarcity of positive effect sizes did not suggest publication bias; however, the small number of studies per outcome limited the ability to detect asymmetry, and imputation-based analyses were not conducted.

This review identified 9 RCTs comparing TECC models with in-person care, 8 of which were hybrid models, and the remaining 1 was a standalone model that was terminated early. We found no clear evidence of an effect of TECC on ECM use less than 6 months. We found a small, statistically significant increase in ECM use at 6-12 months (RR 1.07; 95% CI 1.002-1.130). However, this finding is fragile: the lower bound of the CI only narrowly excludes no effect, meaning that a small shift in events could render the result nonsignificant, and the certainty of evidence is low. Given that the pooled estimates for method use were derived from trials with heterogeneous interventions and low-certainty evidence, the small effect observed at 6-12 months should be interpreted with caution. For other outcomes, including choice of ECM, choice of LARC, LARC use at less than 6 months and 6-12 months, and satisfaction with counseling, the evidence was very uncertain compared with SC. Method switching was assessed in 1 trial [29] but was not reported in sufficient detail to permit analysis. Across outcomes, the certainty of evidence ranged from low to very low. Hybrid interventions dominated the included studies; therefore, no conclusions could be drawn regarding the effectiveness of standalone TECC models.

The included trials were designed to evaluate the superiority of TECC over standard in-person care, not its noninferiority. In contexts where geographic, financial, or structural barriers limit access to in-person CC, a telehealth alternative that achieves equivalent outcomes could still represent a clinically meaningful advance by enabling access to care that would otherwise be unavailable. The current evidence base cannot exclude the possibility that TECC is noninferior to standard in-person care; however, formally demonstrating noninferiority would require adequately powered noninferiority trials with prespecified margins.

In this review, we included only RCTs of tailored, interactive TECC, a definition that has not been used in any previous systematic review. Three previous systematic reviews, all published before 2020 and before the rapid expansion of telehealth during the COVID-19 pandemic, have assessed the effect of telehealth interventions on contraceptive use or choice [11,12,15].

Our primary outcome, ECM use, has been investigated in 1 previous review [11], which included 7 RCTs conducted in LMICs, 3 of which overlapped with our review [23,25,26]. Their meta-analysis showed no overall benefit of telehealth on ECM use compared with SC, but found a small effect in favor of telehealth in a subgroup analysis of 4 studies that evaluated ECM use as a primary outcome. Unlike our review, they included noninteractive interventions and excluded telephone-based interventions. Broader contraceptive use and continuation outcomes have been investigated in a review of telehealth decision aids [12], which included 11 RCTs, 4 of which overlapped with our review [22, 28-31]. Of the remaining 7 studies, 6 did not use SC comparators, and 1 intervention was not tailored. Their meta-analysis showed a small increase in use of any contraceptive method following telehealth contraceptive services compared with controls. Additionally, a recent cluster RCT among Latinx adolescents in the United States showed increased contraceptive uptake with a tailored TECC intervention, but the study was excluded from our review because not all controls received CC [32].

Contraceptive method choice has been evaluated in 1 review that included 5 RCTs, none of which were included in our review because they evaluated noninteractive interventions, such as video-based interventions, and defined their outcome as choice of any contraceptive method [15]. Consistent with our findings, their narrative synthesis showed that telehealth had no effect on method choice in 4 of the 5 trials.

Evidence on satisfaction with and acceptability of telehealth contraceptive services comes predominantly from observational studies conducted in the United States during the COVID-19 pandemic, which consistently report high acceptability, with users valuing convenience and rating counseling quality as comparable to in-person care [8-10,33]. However, a recent evidence map of telehealth sexual and reproductive health studies in high-income settings found that all observational and quasi-experimental studies demonstrated a very high susceptibility to confounding and selection bias, with many relying on convenience samples likely to overestimate acceptability and effectiveness [34]. These findings may also not reflect the experiences of populations with limited digital access or those who prefer in-person care. In LMICs, promising results regarding acceptability have been reported in pilot studies of telehealth communication for contraception among postabortion women in South Africa and among men and their spouses in Uganda [35,36].

This review has several strengths, including adherence to a preregistered protocol, rigorous application of RoB 2 and GRADE, and an exclusive focus on RCTs of interactive and tailored interventions to examine the causal effect of the telehealth counseling modality compared with in-person care. One limitation is the restriction to English-language publications, which may have introduced language bias and excluded relevant non-English-language trials. A further limitation is the exclusion of observational evidence. Prespecification of RCT-only inclusion strengthens causal inference regarding the effect of the telehealth counseling modality but constrains external validity and excludes a substantial body of real-world implementation data that have grown since the expansion of telehealth during the COVID-19 pandemic. Observational studies provide important insights into who accesses telehealth contraceptive services and how these services are experienced, but they are less suited to answering the specific effectiveness question addressed in this review because patients who select telehealth differ systematically from those who attend in-person care with respect to age, language, insurance status, income, and digital literacy. In addition, observational designs in this field have been shown to be highly susceptible to confounding and selection bias [34,37].

We used the standard DerSimonian-Laird random-effects approach in our meta-analysis. The Hartung-Knapp-Sidik-Jonkman method should be considered in future systematic reviews, particularly when the risk of spurious positive findings (type I error) is greater than it was in our analysis. The evidence has important limitations. We did not contact the study authors for additional or clarifying information. Interventions differed widely in content, delivery, timing, degree of provider involvement, and clinical context, potentially contributing to substantial heterogeneity in the results. Outcomes were often self-reported, and group allocation was unblinded, increasing RoB for subjective outcomes such as satisfaction. Some studies were excluded because outcome data did not distinguish between any contraceptive method and ECM as defined in our review. The small number of trials limited subgroup analyses and reduced power to explore sources of heterogeneity through sensitivity analyses. In line with Cochrane guidance, we did not present funnel plots to assess publication bias because fewer than 10 studies were included. We do not suspect publication bias, as most trials showed no effect in favor of the intervention.

Despite our focus on comprehensive TECC, tailoring and interactivity were only partially implemented in most included trials, highlighting a gap in TECC intervention design that may have limited effectiveness. Our review did not assess which components of TECC were most influential in determining outcomes. Previous reviews have attempted to identify the most effective features and have suggested that the incorporation of behavior change techniques and motivational interviewing may increase effectiveness [11,13,14]. However, none were able to determine which specific components were most effective.

The included trials were conducted across antenatal, postabortion, and routine contraceptive care settings, and in both high- and middle-income countries, supporting the generalizability of our findings to some extent. However, important gaps remain: no trial was conducted in a low-income country, and adolescents were represented in only 2 trials [22,28]. These gaps limit the generalizability of the findings to populations with a high unmet need for contraception. Furthermore, only 1 trial [27], which was terminated early, evaluated standalone TECC, highlighting the evidence gap regarding standalone TECC.

Safety outcomes were seldom assessed. One trial reported increased IPV following a mobile-based intervention in Bangladesh [25]. The intervention explicitly encouraged women to discuss contraception with their partners and included content aimed at increasing partner engagement in contraceptive decision-making. Mobile-based interventions that generate records or notifications may inadvertently increase the risk of IPV. This finding underscores the critical importance of prospective safety monitoring, harm-informed design, and safeguard protocols in all TECC evaluations, particularly in settings with a high prevalence of IPV. Although this finding may reflect context-specific factors related to postmenstrual regulation services in a setting with a high prevalence of IPV, it should not be dismissed as an isolated observation. Future TECC trials should consider incorporating routine baseline IPV risk screening, prespecified adverse event monitoring protocols, and context-sensitive content design that avoids prompting partner communication when doing so may increase risk.

Observational studies conducted in the United States have shown that food and housing insecurity, language barriers, lack of insurance, and race are associated with reduced access to telehealth contraceptive care [37,38]. Equity dimensions were not systematically addressed in the included trials, underscoring the need for equity-focused implementation and evaluation in diverse and underserved populations, including individuals with low literacy and limited digital access.

Although the evidence on adjunct TECC is inconclusive, it does not appear to substantially improve use, method choice, or satisfaction in settings where in-person counseling is already available. Our review assessed hybrid TECC in comparison with in-person counseling, which is not available in all contexts. If TECC were noninferior to SC in whatever form that takes, it may offer benefits in settings with limited trained providers, geographical or social barriers to care, or in overburdened health systems. In such settings, even modest effects might translate into population-level impact. The effectiveness of standalone TECC remains unknown, and its clinical relevance would depend on demonstrating that TECC is no less effective, safe, or acceptable than SC.

Future research should prioritize adequately powered evaluations of standalone TECC, including low-income settings and adolescents, and assess long-term outcomes such as continuation, switching, and unintended pregnancy. Noninferiority designs could establish clinical relevance in settings with limited access to in-person care. Mixed-methods approaches are needed to capture user experiences, equity implications, and unintended harms. Standardized and validated measures of contraceptive use, satisfaction, and decision quality would improve comparability. Complementary real-world effectiveness evidence could be generated through rigorous quasi-experimental designs, such as propensity score–matched cohort studies in routine care populations and interrupted time-series analyses that treat system-level changes, such as the COVID-19 telehealth expansion, as natural experiments. The rapid growth of online contraceptive platforms and AI-driven communication requires rigorous evaluation of their effectiveness, safety, and implementation. Evidence is needed to guide decision makers in integrating TECC into routine contraceptive services amid ongoing digital health system transformations.

Current evidence suggests, with low certainty, that adjunct TECC delivered alongside in-person care shows little to no effect on contraceptive use compared with in-person care. For method choice, LARC uptake, and satisfaction compared with in-person care, the evidence was very uncertain. The effectiveness of standalone TECC remains unknown. High acceptability and scalability warrant further rigorous and equity-focused evaluations to inform integration into routine contraceptive services.

All data used in this article are from publicly available published sources. Extracted data are provided in the article and its multimedia appendices. Additional outcome data, risk-of-bias assessments, and statistical calculations for meta-analyses will be made available on reasonable request to the corresponding author (ME). The PROSPERO protocol (CRD42023404402) is publicly available.