IMARA: A mother-daughter group randomized controlled trial to reduce sexually transmitted infections in Black/African-American adolescents.

Black/African-American girls are infected with sexually transmitted infections (STIs) at higher rates than their White counterparts. This study tested the efficacy of IMARA, a mother-daughter psychosocial STI/HIV prevention program, on adolescent Black/African-American girls' incident STIs at 12 months in a 2-arm group randomized controlled trial. Black/African-American girls 14-18 years old and their primary female caregiver were eligible for the study. Girls provided urine samples to test for N. gonorrhoeae, C. trachomatis, and T. vaginalis infection at baseline and 12-months. Mother-daughter dyads were randomly assigned to IMARA (n = 118) or a time-matched health promotion control program (n = 81). Retention at 12-months was 86% with no difference across arms. Both interventions were delivered over two consecutive Saturdays totaling 12 hours. Girls who received IMARA were 43% less likely to contract a new STI in the 12-month post-intervention period compared with those in the health promotion control program (p = .011). A secondary follow-up intent-to-treat analysis provided additional support for the protective effect of IMARA, albeit with a similar magnitude of 37% (p = .014). Findings provide early evidence for IMARA's efficacy, such that IMARA protected against STIs at 12-months among adolescent Black/African-American girls. Future research should examine the mechanisms associated with reduced STIs.

RCT Entities:   Population Interventions Outcomes

Introduction

Youth ages 15–24 years-old account for 50% of new sexually transmitted infections (STIs) annually [1, 2], yet rates vary by race/ethnicity. Black/African-American adolescent females are infected with Chlamydia, gonorrhea, and HIV at 4.5, 10.3, and 20 times that of their White counterparts, respectively [3, 4]. Untreated STIs can lead to serious reproductive health consequences, including pelvic inflammatory disease and vulnerability to HIV acquisition, and high medical costs [5]. Innovative approaches to alleviate STIs among Black/African-American girls are a public health imperative.

Existing STI/HIV prevention programs for Black/African-American adolescent girls and women report small effect sizes, short-term effects, and non-behavioral outcomes (e.g., attitudes, knowledge) [6-9]. Most focus on individual-level behavior change, but social factors influence sexual behavior and STI acquisition [10]. Female caregivers (hereafter referred to as “mothers”) influence daughters’ risky sexual behavior, suggesting the mother-daughter relationship may be leveraged to reduce daughters’ STI risk. Maternal warmth, support and attachment, as well as positive (e.g., open, receptive) mother-daughter communication, are each associated with girls’ reduced sexual risk [11-14], including among Black/African-American adolescent girls [11]. A recent study showed strong mother-daughter relationships and open communication predicted less sexual risk taking among Black/African-American adolescent girls two years later [11]. In light of these findings, mothers may be effective collaborators in preventing STI in daughters [6, 15, 16].

Informed, Motivated, Aware, and Responsible about AIDS (IMARA) is a mother-daughter STI/HIV prevention program for Black/African-American girls guided by a social-personal framework [17] and derived from three evidence-based interventions: Sisters Informing Sisters about Topics on AIDS (SISTA) [18], Sistering, Informing, Healing, Living, and Empowering (SiHLE) [19], and Strengthening the Youth Life Experience (Project STYLE) [20]. SISTA and SiHLE address cultural influences on Black/African-American adult women’s (SISTA) and adolescent girls’ (SiHLE) sexual behavior, labor and power gender divisions, and gender-specific standards for “appropriate” sexual conduct in heterosexual relationships. Randomized controlled trials (RCTs) of SISTA and SiHLE revealed efficacy and areas on which to further strengthen outcome effects. For example, SISTA demonstrated improved self-reported condom use, partner communication, and assertiveness in adult Black/African-American women [18], and SiHLE showed improved condom use and fewer sex partners in adolescent Black/African-American girls [19]. However, neither SISTA nor SiHLE address mental health or the mother-daughter relationship and communication, and findings from SISTA do not report biological outcomes. Project STYLE is complementary to SISTA and SiHLE; it addresses STIs while emphasizing the role of mental health (having been designed for adolescents in psychiatric care) and demonstrated improved parent-teen sexual communication, parental monitoring, and adolescent reported condom use [20]. However, Project STYLE does not focus on the role of gender or racial/ethnic empowerment or report biological outcomes. IMARA was therefore designed to address the gaps in each program by combining their strengths to reduce STIs in Black/African-American adolescent girls.

This study sought to provide the first test of IMARA on Black/African-American adolescent girls’ STI acquisition over one-year. As detailed below, 199 mother-daughter pairs were randomly assigned to IMARA or a time-matched health promotion control program. We hypothesized that girls who received IMARA would be less likely to contract a new STI at 12-months than girls in the control group. The study is positioned to provide early but rigorous evidence for an innovative approach to alleviating STIs among Black/African-American adolescent girls, and lay the foundation for future investigation into the mechanistic pathways underlying STI prevention in this group.

Methods

Procedures

Participants were 199 Black/African-American girls 14–18 years-old (M = 16.02; SD = 1.35) and their female caregivers. Girls and their caregivers were recruited through two strategies to maximize generalizability and represent a broad range of mental health problems from 11/2012–04/2016. The final follow-up assessment was completed on 06/2017. First, dyads were recruited from mental health clinics, whereby clinic staff hired by the study served as liaisons to the research team. The clinic liaisons identified and presented the study to eligible mothers and/or daughters, and with familial consent, provided their contact information to the research team. This approach was used to enroll 41% of the sample. Second, research staff conducted street outreach, distributing study fliers at community programs, street fairs, and school fairs, collecting names and numbers of interested families, and successfully enrolled 59% of the sample. Inclusion/exclusion criteria was the same across recruitment venues/approaches. In both cases, staff followed up by telephone to provide more information and schedule baseline assessments and the intervention. Upon arrival at the research site, mothers and daughters met separately with researchers to review consent and assent forms, including information about trial design (e.g., random assignment) and confidentiality of girls’ STI results (i.e., mothers learned they would not be told). The baseline assessment was completed within 8 weeks pre-intervention to allow time to assemble groups. However, 54% of dyads completed the baseline the same morning of day 1 of the IMARA/health promotion program.

On the morning of workshop day 1, dyads were randomly assigned to the IMARA (n = 118) or the health promotion control program (n = 81) as follows. Upon arrival, daughters selected a slip of paper from a bag that indicated their group assignment (IMARA vs. health promotion control). Dyads were not assigned to groups in advance of workshop day 1 to prevent attendance bias due to group assignment. We employed two randomization strategies depending on the number of dyads present on workshop day 1. Where ≥ 8 dyads were present at the start of the workshop (52% of dyads), we used a 1:1 randomization ratio; girls selected the slips of paper and were evenly randomized to treatment arms. Where ≤ 7 dyads were present (48%), we delivered a single program to ensure a sufficient group size. There was one exception where 5 dyads were randomized to two arms. The project director, but not the recruiters, were aware which intervention would be delivered in the event there were too few dyads (< 8) to randomize to both arms. In general, we alternated between IMARA and the health promotion condition, but in the final year of recruitment we favored IMARA to enhance analytic power to detect treatment effects and to provide a large enough sample to evaluate mechanisms associated with key outcomes in IMARA. Although originally unplanned, these strategies led to an overall randomization ratio of approximately 1.5:1 favoring IMARA. The CONSORT diagram (Fig 1) illustrates the number of dyads randomized to arms and their retention at 12-month follow-up.

Fig 1

Consolidated standards of reporting trials (CONSORT) summary of participant enrollment and retention at 12-month follow-up.

Both programs were delivered in groups ranging from 1–9 dyads over two consecutive Saturdays at the research site for a total of 12 hours (approximately 6 hours each day). Dyads completed a 12-month assessment post-baseline either at the research site or a location convenient for the family. Compensation for all research activities totaled $165 per participant plus reimbursement for travel. The study was approved (#2011–0263) by the University of Illinois at Chicago on 06/08/2011. This trial is registered at Clinicaltrials.gov (NCT02958813). Registration was delayed until 1½ months following the publication of the 2016 Final Policy on the Dissemination of NIH-funded Clinical Trial Information. Up to that point, NIH-funded studies were not required to register, and it was unclear whether the current behavioral study qualified because it did not involve experimental drugs. The Final Rule’s publication expanded and clarified registration requirements, thereby prompting registration. The authors confirm that all ongoing and related trials for this intervention are registered at Clinicaltrials.gov.

Participants

Adolescent girls were eligible if they: a) were 14–18 years old; b) self-identified as Black/African-American; c) had a primary female caregiver (“mother”) who lived with them; d) understood and provided consent/assent; e) spoke English (measures were normed for English speakers and the intervention was delivered in English); and f) had parental consent. Mothers were eligible if they: a) self-identified as Black/African-American; b) identified as the adolescent’s primary female caregiver; c) were > 18 years old; d) understood and provided consent; and e) spoke English (measures were normed for English speakers and the intervention was delivered in English). Girls were excluded if they were actively psychotic or severely mentally ill. No girls were excluded based on this criteria.

Measures

The AIDS Risk Behavior Assessment (ARBA) [21] was administered at baseline with other measures not included in this study. The ARBA is a widely-used computerized voice-assisted self-administered interview of sexual behavior. Girls reported whether they ever had vaginal/anal sex (yes/no). Those who indicated lifetime vaginal/anal sex were prompted to indicate if they had vaginal/anal sex in the past six months (yes/no), and if they used a condom at last vaginal/anal sex (yes/no).

At baseline and 12-months, girls provided urine samples to screen for N. gonorrhoeae, C. trachomatis, and T. vaginalis via nucleic acid amplification testing. We used the Abbott Real Time CT/NG assay, and the Taq-Man PCR for TV. We did not test for HIV given the low prevalence in adolescents, instead using STIs as a proxy for unprotected sex. STI-positive girls were offered free, single-dose, directly-observed therapy. Consistent with Illinois law, expedited partner therapy was offered. The study physician was unable to confirm partner therapy, but treatment was confirmed for 92% (n = 33/36) of girls at baseline: 31% were treated by the study physician, and 61% were treated by another source verified by research staff via conversations with providers, name of the provider or clinic, and/or description of the medication. Treatment rates did not differ by intervention arm. We were unable to verify treatment of three participants (two assigned to IMARA and one to the health promotion program), and thus their data were excluded from the outcome analyses that relied on known STI status.

Intervention and health promotion control programs

IMARA and the health promotion control programs were similarly structured. Both programs occurred in groups over two workshop days (12 hours total) separated by one week. Parts of the curriculum were delivered separately to mothers and daughters covering parallel content, and parts of the curriculum brought dyads together in a single group. Participants in the two programs did not overlap. For each program, two facilitators co-led the mothers’ group and two co-led the girls’ group. All four facilitators co-led mother-daughter joint activities.

Informed motivated aware and responsible about AIDS

IMARA was derived from three evidence-based interventions (SISTA; SiHLE; Project STYLE), guidance from a long-standing community advisory board, and pilot testing. Activities from each of the three curricula were evaluated and selected for inclusion based on the goals of the intervention. For example, the parent-teen communication components from Project STYLE were included to strengthen mother-daughter communication, whereas the female empowerment content of SISTA and SiHLE was incorporated to address gender and ethnic pride [18, 19]. Pilot testing with 22 caregiver-daughter dyads provided strong evidence of acceptability and feasibility by girls and their caregivers.

IMARA’s curriculum focuses on strengthening mother-daughter relationships and communication, particularly regarding STI/HIV prevention and safer sexual behavior, increasing self-efficacy to use condoms, improving maternal monitoring, promoting pride in Black/African-American culture and encouraging gender empowerment. Mothers and daughters learn and practice assertive communication through role-plays and games, discuss healthy versus unhealthy relationships with peers and partners, receive facts about STIs and HIV, consider the role of media in Black/African-American girls’ self-image, and identify the impact of mental health on risky sexual behavior.

Morning and afternoon sessions begin with all mothers and daughters together in the same group and an icebreaker to enhance ethnic and gender pride. Next, mothers and daughters are separated into their own groups and discuss the impact of marketing and music on perceptions of Black/African-American adolescent girls. Mothers develop monitoring plans to augment oversight of their daughters, and girls identify triggers (people, places, moods, situations) of risk behavior and create personalized plans to manage the triggers. In separate groups, mothers and daughters review safe sex knowledge and attitudes and learn new skills (e.g., condom use). Interactive and experiential activities are designed to catalyze discussions of physical, emotional, and sexual abuse in relationships and the impact of emotions and relationship power imbalances on STI/HIV-risk. Mothers and daughters come together for joint activities designed to strengthen mothers’ credibility as a resource for STI/HIV prevention and facilitate communication skills practice. Dyads discuss challenging topics to improve conflict negotiation and assertive communication and receive feedback from group members.

Health promotion control

We compared IMARA to a health promotion control program matched in length, intensity, and time spent in joint mother-daughter activities to control for non-specific therapeutic effects associated with contact time, group relationships, and facilitator attention. However, we ensured that the content of the program did not address sexual and reproductive health or mother-daughter communication, the active ingredients hypothesized to impact outcomes in IMARA. The health promotion program emphasizes healthy eating and nutrition, physical activity and exercise, informed consumer behavior, beauty standards for Black/African-American women and girls, personal and societal facts and costs of drug/alcohol use, and violence prevention. The curriculum is based on a health promotion program used in prior research [22], but adapted to ensure topics addressed important general health concerns in the target population–urban Black/African-American women and girls. Similar to IMARA, the health promotion curriculum employs an interactive approach, using games, videos, factual presentations by facilitators, and hands-on activities (e.g., planting herbs for nutritional benefits). Mothers and daughters learn relaxation exercises and how to understand nutritional labels. During joint activities, mother-daughter dyads discuss media images of beauty, watch videos, play games, and develop physical activity pyramids. In contrast to IMARA, mothers and daughters did not engage in role-plays or joint communication exercises, and they did not receive condom skills training. Specifically, IMARA participants learned the steps of condom use, practiced putting a condom on a penis model, and received feedback from facilitators and group members to ensure accuracy. By contrast, the health promotion participants watched a 10-minute video demonstrating condom use. The only overlap between IMARA and the health promotion content was a 15-minute game of Jeopardy to review the facts of STI/HIV transmission and prevention. We decided to provide STI/HIV information and a video of condom use given the high-risk profile of the population, although we recognize this may have attenuated group comparisons.

Facilitator training

Facilitators in both IMARA and the health promotion program were Black/African-American women with backgrounds in psychology, Bachelors or Master’s degrees, previous experience leading groups and working with youth in health settings. Facilitators did not overlap arms and were trained separately. Facilitators in both arms were trained in groups over a month (30 hours total). Training was led by the project director and an experienced facilitator with graduate-level education. Where possible, facilitators also observed at least one full workshop prior to delivering the program, and in all cases, new facilitators were paired with an experienced facilitator to lead their first two workshops. Training reinforced the importance of manualized interventions, following intervention content, and techniques to encourage girls’ and mothers’ participation. Facilitators practiced each session, conducting “mock run-throughs,” and received extensive feedback until deemed competent by the project director. Training also included the facts of STI/HIV transmission and prevention, adolescent psychosexual development, group dynamics, and behavior management.

IMARA fidelity

To evaluate treatment fidelity to the IMARA curriculum, facilitators rated their adherence to curricular activities at the end of each workshop. Ratings were reviewed by the project director following each workshop session and discussed during supervision along with any concerns and need for additional training. Annual refresher trainings were conducted to prevent facilitator drift from the curriculum. Treatment fidelity based on facilitator reports was 97%.

Data analyses

Power analyses determined the sample size needed to identify differences in the presence of a new STI at 12-month follow-up among participants from IMARA versus the health promotion control group. Our registered, a-priori power calculations were conducted assuming a 1:1 randomization scheme: Using a two-sided test with alpha = .05, a sample of n = 200 would yield ≥ 80% power to detect a relative risk of ≤ 0.40 for the two-group comparison, with new STI prevalence in the control group at 25%. Power was not substantially altered when assessed retrospectively for a 1.5:1 allocation favoring IMARA, as was ultimately arrived at in the present study.

Log-binomial regression was used to test differences between arms in the presence of a new STI at 12-month follow-up, adjusting for the presence of any STI at baseline. The new STI outcome at follow-up was a binary variable (yes/no to testing positive for at least 1 of the 3 STIs), because the study was not powered to examine specific STI outcomes. Standardized differences in means or proportions were calculated between arms for each baseline variable. All standardized differences were small (< |.20|), and thus, covariates were not included in the regression models, except for baseline STI status (yes/no). This exception was made for consistency with existing literature: past STI occurrence is strongly associated with future acquisition, and so it is standard to co-vary for STI history when predicting future infection. We conducted the log-binomial analyses in two ways. (1) Consistent with the original analytic plan registered at Clinicaltrials.gov, we ran the model among only those participants who provided all STI data, and for whom STI status could thus be known at both time points (n = 164). (2) We also conducted a follow-up intent-to-treat analysis in which participants with missing follow-up data were coded according to their baseline STI status. This approach, also known as the last observation coded forward method, provided a more conservative check on the original modeling. Robust variance estimation (sandwich estimator) accounted for correlations among participants within clusters (i.e., groups in which dyads participated) in all models. Note that log-binomial regression is appropriate for estimating the relative risk of a binary outcome that is not infrequent (e.g., occurring in > 5% of cases). All log binomial models were re-run including an interaction between arm and baseline STI status in order to evaluate if any intervention effects were moderated by baseline STI status. The interaction term was small and non-significant in each case, failing to provide support for significant moderating effects. We thus present findings from the models without the interaction term. All analyses were performed using SAS version 9.4.

Results

Fig 1 shows participant flow. Of the 670 dyads screened, 142 (21%) were ineligible primarily due to the girl not meeting the age requirements and/or the family being unable to attend sessions. Of the 528 eligible families, 174 (33%) declined to participate, and 98 (18%) did not have working telephone numbers to schedule appointments. Thus, 256 dyads completed the baseline assessment. Consistent with previous research [20], attrition between baseline assessment and intervention start was 22% consisting of families no longer interested (2%) and families who were scheduled but did not show up (20%). This resulted in 199 dyads randomly assigned to IMARA or the health promotion program. Retention at 12-months was 84% for IMARA and 90% for the health promotion program and did not differ between arms (Fig 1).

Table 1 presents baseline descriptive statistics for the sample. Caregivers were biological mothers (64%), aunts (16%), grandmothers (11%), other (5%), and adoptive mothers (4%), ranging in age from 21–75 years (M = 42.82; SD = 10.36), and 78% reported family earnings <$30,000 annually. Over one-third of the girls (38%, n = 74) reported ever having had vaginal/anal sex at baseline. Of these, 74% (n = 55) reported vaginal/anal sex in the past six months, and 42% (n = 31) indicated not using a condom at last vaginal/anal sex. Notably, within the subsample positive for a STI at baseline, only 66%, (n = 23) indicated lifetime vaginal/anal sex. Of these, 70% (n = 16) reported vaginal/anal sex in the past six months, and 43% (n = 10) reported not using a condom at last vaginal/anal sex. Caregiver type was not significantly associated with testing STI-positive at baseline (p >.05). Percentages reflect available data.

Table 1

Descriptive statistics in girls at baseline.

	Full Sample
Variable	Total (n = 199)	IMARA (n = 118)	Control (n = 81)
	Mean (SD)	Mean (SD)	Mean (SD)
	or % (n)	or % (n)	or % (n)
Sexual Risk
Positive for any STI	19% (36)	21% (24)	15% (12)
Mean number of STIs	0.21 (0.48)	0.25 (0.52)	0.16 (0.40)
Ever had sex	38% (74)	38% (44)	38% (30)
Sexually active in past 6 months*	74% (55)	77% (34)	70% (21)
Condom use at last sex*	58% (43)	59% (26)	57% (17)
Demographics
Age at baseline (years)	16.02 (1.35)	16.07 (1.41)	15.95 (1.26)
Black/African-American race	99% (197)	99% (117)	99% (80)
Hispanic ethnicity	2% (3)	0% (0)	4% (3)
Mother lived on less than $30,000	78% (155)	77% (91)	79% (64)

Note. All standardized differences between arms in the means or proportions for each variable were < |.20|. Possible number of STIs ranged from 0–3. Ever had sex indicated lifetime vaginal/anal sexual activity. Sexual activity in the past 6 months and condom use at last sex both referred to vaginal/anal sexual activity. Financial data were collected from mothers and reflected amount lived on over the past year. All percentages were calculated based on available data.

*Sexual activity in the past 6 months and condom use were assessed only in the subset of girls who reported ever having been sexually active: n = 74 in the full sample, n = 44 in IMARA, and n = 30 in Control.

Regarding mental health, 26% and 27% of the sample self-reported clinically significant externalizing and internalizing symptoms on the Youth Self-Report [23] at baseline, respectively. These rates did not differ significantly between arms (p >.05). For an in-depth summary of mental health symptoms in the sample, including the effects of IMARA on externalizing and internalizing symptom trajectories over 12 months and the associations of symptom change with the protective effect of IMARA against future STIs, see Kendall et al. [24].

As noted, this study was not powered to test the effects of IMARA on specific types of STIs. For descriptive purposes, however, we calculated the prevalence rates of each STI. At baseline among girls in IMARA, prevalence rates for chlamydia, gonorrhea, and trichomoniasis were 13% (n = 15), 3% (n = 3), and 9% (n = 10), respectively. At 12 months, these respective rates were 8% (n = 8), 3% (n = 3), and 7% (n = 7). Among girls assigned to the control arm, baseline rates of chlamydia, gonorrhea, and trichomoniasis were 9% (n = 7), 4% (n = 3), and 4% (n = 3). These respective rates at 12 months were 15% (n = 11), 4% (n = 3), and 11% (n = 8). Girls could test positive for more than 1 STI. Among girls who tested positive for at least 1 STI at baseline, 37% (n = 13) reported having ever been told by a medical provider that they were STI-positive; of those, 54% (n = 7) had been delivered this news in the past 6 months. At 1 year, 12% (n = 4) of girls who tested positive for a STI indicated they had been told by a provider outside of the study about their status. All percentages were calculated based on available data.

Girls attendance at both sessions of IMARA and the health promotion program was 80% (n = 160). Partial attendance did not differ across intervention arms; 24% in IMARA and 14% in health promotion program, χ2 (1, 198) = 2.78, p = .103. Reasons for non-attendance included scheduling conflicts, illness/hospitalization, childcare, and transportation/car problems. At 12-month follow-up, there were no significant differences in missing STI outcomes by intervention arm (19% IMARA vs. 11% health promotion; p = 0.122).

Prospective analyses tested the difference between conditions in a new STI at 12-months, adjusting within the same model for baseline STI status and cluster robust standard errors. Among girls who provided STI data at both time points (n = 164), the risk of a new STI at 12-months was 43% lower for girls from IMARA than the health promotion program, relative risk (RR) = .57, 95% confidence interval (CI) [0.37–0.88], p = .011. Within this same model, the effect of the baseline STI status covariate on STI acquisition by 12-months was RR = 3.24, 95% [CI 1.78–5.93], p<.001; that is, people who were STI-positive at baseline were much more likely to have an incident STI at follow-up. Among girls with observed data at each time point, STI rates in IMARA went from 19% (n = 18) at baseline to 16% (n = 15) at 12-months, and rates went from 14% (n = 10) to 24% (n = 17) in the health promotion program (Fig 2).

Fig 2

STI prevalence rates at each time point.

STI prevalence rates among girls with observed data at both time points at baseline (n = 18/93 in IMARA; n = 10/71 in the control group) and 12-month follow-up (n = 15/93 in IMARA; n = 17/71 in the control group). Error bars indicate the standard error of the probability within a given arm.

Next, we ran a follow-up intent-to-treat analysis with the last observation coded forward for n = 192 participants to provide a more conservative evaluation of treatment effects. Seven participants were excluded from this analysis, three participants with unconfirmed STI treatment at baseline and four participants who were not tested at baseline. This method also provided support for a significant protective effect of IMARA against future STIs, RR = 0.63, 95% [CI 0.43–0.91], p = .014. Within this model, the effect of the baseline STI covariate was RR = 4.39, 95% [CI 2.49–7.74], p<.001.

Discussion

This study provides preliminary efficacy data indicating that IMARA protects against incident STIs at one-year follow-up among Black/African-American adolescent girls. In a 2-arm group RCT with conditions matched in time and intensity, girls from IMARA showed a 43% lower likelihood of a new STI compared to those in a time-matched mother-daughter health promotion control program. Given the preliminary nature of the data, and the potential for spurious effects, we followed up with a more conservative intent-to-treat analyses by assigning youth with missing outcome data the same STI status as their baseline. This approach also showed that IMARA was associated with a significantly lower likelihood of future STI acquisition compared with the control arm, albeit with a weakened magnitude (37%) compared with the original model. Findings advance previous research by producing strong effect sizes and treatment effects on biologically determined STIs over 12 months for Black/African-American adolescent girls, who are at elevated risk of STI/HIV relative to White and Latina peers [4, 25].

Prior research has been limited by short-term effects (e.g., 3 or 6-month follow-up) [6, 16], non-behavioral outcomes (e.g., attitudes, beliefs) [7], and self-reported sexual behavior [8, 9]. SISTA and Project STYLE did not report biologically determined STI outcomes [18, 20], the primary outcome of this study, but they did demonstrate change in self-reported sexual behavior. Like IMARA, girls who received SiHLE were less likely to acquire a new chlamydia infection over 12-months than girls in the comparison group. However, SiHLE was delivered over four Saturdays, a potentially more burdensome schedule, compared to IMARA’s two-day workshop, and SiHLE did not include girls from mental health clinics–a uniquely challenging and vulnerable population. Future research should compare the treatment effects and cost-effectiveness of active HIV prevention programs to determine the best use of limited resources.

Several factors may explain our positive effects, but future research must formally test mediators. IMARA builds on a social-personal framework [17] and empirical findings [11, 13] emphasizing the central role of mothers in daughters’ sexual development and decision-making. By focusing on the mother-daughter dyad, IMARA leverages an important social resource for girls and contributes a new strategy to the STI/HIV prevention toolkit [26]. IMARA aims to change girls’ behavior in part by strengthening daughter’s perceptions of mothers as a support system in sexual decision-making, and by shifting mothers’ and daughters’ peer norms within the group in favor of prevention. IMARA’s focus on building relationships may be particularly salient for adolescent girls as increased technology is minimizing human connections.

IMARA builds on previous findings that strong mother-daughter communication is related to less adolescent risky sexual behavior, [11, 12, 14] with facilitators teaching dyads to communicate effectively about sexual topics. In doing so, IMARA may set the stage for continued conversations as girls reach new developmental milestones. This may explain why IMARA’s positive effects were observed out to one year after the workshops; testing if improvements in mother-daughter communication mediate IMARA’s intervention effects is important for future inquiry.

Finally, IMARA targets individual and social mechanisms shown to affect sexual behavior and these may help explain the reduction in STIs. For example, mental health [27], greater relationship power [28, 29], increased ethnic and gender pride [30], and stronger emotion regulation [31] may influence STI outcomes. IMARA promotes mothers as role models for daughters, demonstrating pride in womanhood and Black/African-American identity, cautioning girls about the imbalance of power in age-discrepant relationships, and supporting emotion regulation strategies that improve safe-sex decisions. Indeed, recent work from our group using the same sample as in the present study showed that among girls who entered with high versus lower externalizing mental health symptoms, those who received IMARA showed a significantly greater decrease in externalizing scores relative to the control group [24]. Furthermore, among these girls, symptom improvements appeared to be associated with IMARA’s protective effect against new STIs, suggesting that mental health change might mediate the intervention effects. Future study should formally evaluate the role of mediators of IMARA’s positive STI treatment outcomes.

Notably, 34% of STI-positive girls at baseline reported never having had vaginal/anal sex. This is consistent with other studies [32]. It is possible that girls did not understand the questions, were unable to recall prior sexual experiences, were reluctant to report sexual activity because their caregiver was involved in the study, or had a narrow definition of sexual behavior that excluded certain activities (e.g., anal sex). Likewise, girls may not have endorsed unwanted sex or simply preferred not to disclose. Findings underscore the unique value of biological outcomes relative to self-reports. Future studies should seek to understand the discrepancy between objective and self-reported data and identify ways to improve the validity of self-reports, perhaps through integration with biological markers [32]. Diminished socioeconomic resources heighten risk for STIs and HIV [33, 34], yet IMARA appears to have protected against STIs in girls despite these structural challenges, as 78% of mothers reported < $30,000 annual family income, and 75% indicated being single parents.

Study limitations should be considered in light of these promising effects. This study represents a single test of IMARA; replication is required. Mothers and daughters were not blinded to condition because intervention content revealed assignment status. However, the interventions were matched in length, intensity, and amount of time mothers and daughters spent together to control for these non-specific factors. Results pertain to Black/African-American adolescent girls and their mothers and may not generalize to other groups. Patterns may differ depending on the type of caregiver. Future studies with greater power could perform a stratified analysis to unpack if caregiver type (e.g., biological mother, aunt) is related to the intervention effects. As with many efficacy trials where participants are compensated to participate in an intervention, this study reimbursed mothers and daughters each $40 to attend each 6-hour workshop day. Providing compensation may limit the feasibility of participation outside the research study, but the small amount–about $7 per hour–was designed to be non-coercive and offset the potential for lost wages. Observed differences in STI rates between groups at one year may suggest girls in IMARA were more likely to be tested and treated during the 12-months following the intervention. This alternative interpretation, however, still supports IMARA’s benefits since testing and treatment are themselves important public health outcomes. We did not test participants for HIV, because of the low incidence among adolescent girls. However, STIs are a proxy for unprotected sexual activity, a known risk for HIV. Despite limitations, the study has several strengths, namely use of biological STI outcomes, long-term follow-up, and strong effect sizes.

Few STI/HIV evidence-based interventions for Black/African-American adolescent girls translate into “real-world” settings. Next steps will require careful attention to the factors influencing IMARA’s reach, adoption, implementation, maintenance and dissemination [35]. IMARA’s length and number of facilitators may present barriers to dissemination and implementation, particularly in resource-poor environments. However, by delivering IMARA over two days, we sought to lessen family burden from more typical multi-session weekly interventions. Moreover, as a first test of IMARA, the evidence of effectiveness in this study can serve as a springboard for future adaptations for specific settings and contexts. Two examples are currently underway; we are exploring the feasibility and effectiveness of a one-day workshop, and we are adapting IMARA for the South African context. Partnering with setting-specific stakeholders will drive adaptation (e.g., length, content), delivery (e.g., format, number of facilitators), and evaluation. Additionally, adaptive designs [36] can test and distinguish the potent components of IMARA to create a streamlined curriculum. Likewise, evaluating alternative implementation approaches (e.g., embedding IMARA in sexual health services, schools, faith-based organizations) can inform optimal delivery. Finally, IMARA can be adapted to include new prevention technologies to alleviate STI/HIV stigma and improve prevention behavior.

(XLSX)

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(DOC)

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23 Jan 2020

PONE-D-19-32194

IMARA: A mother-daughter group randomized controlled trial to reduce sexually transmitted infections in Black/African-American adolescents

PLOS ONE

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Reviewer #1: The authors conducted a randomized controlled trial to reduce sexually transmitted infections in Black/African –American adolescents. I found the paper to be written well with a clear logical flow and tight focus. However, I have identified minor concerns that the authors should work on.

Methods Line 97-99,page 5 Why was the mental health clinic targeted for the initial enrollments? Why this sampling strategy? This may suggest that the study team was more interested in a vulnerable population who definitely may have relational issues with their mothers/caretakers. This could potentially bias the effect of the intervention making it appear positive when it is not. Are you able to describe what mental health problems they had to assure the readers that this would not bias your findings?

Line 113, page 6 What do you mean by dyads learned their group assignment after the baseline assessment....? Make this sentence clear to the reader.

It is not clear whether the curricular used were hard copies or soft copies on tablets etc. Relatedly, the inclusion criteria ....spoke English.... do the interventions need one to speak English only without reading? Did you do any language proficiency testing for these adolescents?

Line 141, noted rationale for not doing HIV testing but given the strong association between HIV transmission and STIs; at the subset of adolescents that had STIs at 12 months should have received HIV screening. Are the authors able to get this data and include it? may be from a related program etc

Line 143-144,page 7 consistent with Illinois law, expedited partner therapy was offered. Please provide a citation or describe what procedures are done to ensure partner was offered therapy. Also make clear for how long treatment for the STIs was?

Line 164, add a citation in support of this information.

Line 165-166, page 8- was this work re acceptability and feasibility published?if yes provide a citation.

Line 180 Mothers and daughters separately review..... is this referring to the mother and daughter dyad? please make clear

Line 203 - .... and they did not receive condom skills training. I find this quite surprising in this day and age. Line 205 refers to a 10 minute video demonstrating condom use. How different is the content of this video and the condom skills training? Please clarify

IMARA Fidelity

Noted facilitators rated their adherence to curricular activities. What was fidelity based on the directors report?

Results

Did the STI risk differ with type of caregiver?

Lines 275-279- State the reasons for non attendance as they may be related to the intervention thus affecting feasibility.

Describe what STIs were identified at baseline and at 12 months. Do they differ? Were there any negative outcomes from the intervention e.g caretaker violence, depression, daughter withdrawal etc

Discussion

Line 312 Describe what you mean by advance previous research? may need to reword

Line 314, describe the short term effects and non behavioral outcomes. How do they differ from what the IMARA intervention resulted into?

Line 339- treatment outcomes - clarify which treatment (IMARA or the STI treatment)

Line 360.... in IMARA were more likely to be tested and treated during the 12 months following intervention. This introduces surveillance bias. Can the authors describe how this bias was overcome as it affects the main study outcome.

References- Have the citations in brackets as per PLOSONE reference style.

Reviewer #2: This paper presents the results of a randomized controlled trial that evaluates an intervention for African-American teenage girls and their mothers/caretakers. The strengths of the research include a clearly described intervention (and control), good number of study participants, with excellent follow-up rates. This much have been a very challenging study to set up, conduct and implement. The limitations of the study include apparently contradictory findings in crude vs. adjusted analysis, and limited information on any outcome other than STI rate itself.

Specific comments follow.

Overall. The introduction is good. A line or two could be added to describe the potential “mechanisms” by which this intervention might reduce STIs – would it be due to less sex, increased condom use, or lower risk partners?

Can the authors include the specific trial number for clinicaltrials.gov?

Could be helpful to understand how much participants were paid to attend the workshops, to help understand its feasibility outside of a research study.

It would be helpful to know what diagnostic test kit was used to test for chlamydia, gonorrhea and trichomonas (and whether there could be false positives).

Results –

Can the authors present which specific infections were actually diagnosed – did this intervention reduce chlamydia and gonorrhea and trichomonas? – or was most of the effect related to trichomonas?

Were there any questions about self-reported STIs diagnosed outside of the study between baseline and follow-up? Or questions about possible mediators such as self-reported sexual behavior at 12-month followup? Or mother-daughter discussions about sexual behavior?

It remains a bit unclear what conclusion to make when the unadjusted RR was 0.59 (lower risk), and the adjusted RR was 3.2 (higher risk when comparing to baseline status). This conflicting finding should be discussed more in the discussion. If there was an “a-priori plan” to adjust for baseline STIs included in the clinicaltrials.gov protocol, then the authors should probably be focusing on that result (which showed an increased risk in the intervention group).

Minor issues –

Methods – the description of the randomization could be more clear how more people were randomized to the intervention – and could refer to the consort diagram (optional – this is presented in the results but could be in the methods).

Minor – line 246 clarify if the “treatment” refers to the participation in the intervention (or some other sort of treatment…)

Minor – Table 1 – more clarify the denominators for the percentages for “sexually active last 6 months and condom use” (mentioned in the footnote, but not obvious when first reading through the table).

Reviewer #3: This is an important randomised controlled trial testing the efficacy of the IMARA project (a mother-daughter psycho-social STI/HIV prevention program) vs. a control arm of a more generic intervention promoting healthy eating and nutrition, physical activity and exercise, in a group of 199 adolescent Black/African-American girls’ incident STIs at 12 months.

This study provides preliminary efficacy data indicating that IMARA did protect against the primary endpoint of incident STIs at one-year follow-up.

However, there are aspects of the study design and analysis that could have confounded the results and which need to be clarified before drawing firm conclusions on the efficacy of this intervention. This is key before implementing similar program in other target populations.

Main points

1. Randomisation schedule was created in an unusual way. Dyads were asked to select their randomisation treatment from a paper bag. This could have led to systematic bias and Table 1 indeed shows large imbalances for some of the participants’ characteristics at baseline (e.g. % positive for STI, mean number of STI, ethnicity, history of sex and socio-economic status). These are key common causes of both treatment allocation and incidence of STI so could have confounded the results. Authors should re-perform the analysis after controlling for all these additional imbalanced factors not just for the presence of STI at baseline. Residual confounding should be also mentioned in the limitations (lines 356 onward).

2. Similarly, the procedure of alternating between IMARA and the health promotion program would have made the process predictable and broke down the concealment of allocation so that recruiters could have decided not to enrol, say, a problematic dyad if it was known that next allocation would have been for example control and not IMARA.

3. Mothers and daughters in the control arm did not engage in role-plays or joint commune exercises, resulting in lack of blinding. Unclear why efforts were not made to try to implement blinding. This is an additional limitation that should be mentioned in the Discussion.

4. Calculation of statistical power is cryptic. It is said that dyads were randomly assigned to the IMARA (n=118) or the health promotion control program (n=81) following an overall ratio of roughly 1.5:1 favouring IMARA to enhance analytic power to detect the treatment effect. Nevertheless, in the Methods power is given for a total sample size of N=200 participants, assuming an even split of 100 vs. 100 in the 2 groups. Authors should show the difference in power using the 1:1 vs. the 1:1.5 random allocation and explicit reasons for choosing the latter. What was the expected increase in power? In general, from the text in lines 251-258, it appears that the sample size of 199 resulted as a consequence of an inevitable attrition between baseline assessment and initiation of the intervention rather than a pre-planned design.

5. Although similar by treatment arm, the rate of non-adherence/loss to follow-up was not negligible at 16% and 10% in the two arms. Because of that it is possible that the two groups are no longer exchangeable at 12 months. It is not an unreasonable assumption in these settings that daughters who are lost to follow-up are more likely to be have acquired STIs. Authors should perform an intention to treat analysis using the missing-failure approach. Alternatively, it is possible that the effect of the strategy could have been diluted by attrition so authors should also perform an on-treatment analysis after controlling for post-baseline confounding factors using a marginal model. This should control for all possible post-baseline prognostic factors as well as common causes of acquiring STI and risk of drop-out.

6. Lines 264-273. The issue of baseline exchangeability between arms is ruled out in the Methods with a couple of sentences saying that there was no difference at baseline between the two groups. A p-value >0.05 for these comparisons (line 236) is meaningless and should not be reported as this p-value should be equal to 1 as the null hypothesis is true by definition in a trial. On the other hand, there are larger imbalances between baseline factors which should be described in the text and controlled for in the analysis. For example, mothers in the IMARA arm were less likely to earn <$30k per annum that mothers in the control arm and this could have explained the difference in incidence of STI at 12 months. The sentence that overall >75% (which becomes ‘almost 80%’ in line 351 of Discussion section) of mothers earned <$30k annually in both groups is inaccurate and misleading.

7. Line 288. This same model adjusted for baseline STI status was RR=3.24, 95% [CI 1.72-6.11], p=.000. Has the direction of RR being inverted? Is this the difference of control vs. IMARA?

8. The fact that the difference observed could be due to mediators is mentioned and several potential mediators are listed e.g. improvements in mother-daughter communication etc. Was use of condom measured in the study? Change in sexual risk behaviour seems to be the most obvious surrogate endpoint/mediator in this analysis to verify.

9. Line 359. American adolescent girls and their mothers and may not generalise to other groups. Patterns may differ depending on the type of caregiver. For how many dyads the caregiver was not the natural mother? Unclear why a stratified analysis by type of caregiver (mother vs. other) could not be performed.

10. What was the effect of SISTA SiHLE and STYLE compared to this intervention? Results of the various trials should be reported and compared in the Discussion section.

Other points

1. Lines 248-250. This stringent approach was not intended to be fully powered, but rather to provide a preliminary check of whether the pattern of results observed within the full sample replicated within the subset known to be sexually active at baseline. Indeed, it is very likely to actually be under-powered. Would have been more sensible to restrict the analysis to those who did not show STI at baseline?

2. Line 306. Suggested rewording: This study provides preliminary efficacy data indicating that IMARA protects against incident….

3. Line 308. The authors claim that for consistency with existing literature past STI occurrence is strongly associated with future acquisition, and so it is standard to co-vary for STI history when predicting future infection. Nevertheless, the unadjusted RR of 0.43 is mentioned here, why?

4. Line 341. Suggested rewording: It is possible THAT girls did not understand the….

If the data are consistent with the literature, why is paragraph (in lines 341-349) needed at all? Or is it instead the case that 33% is likely to be an under-estimate of the prevalence of STI at baseline?

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Reviewer #1: No

Reviewer #2: No

Reviewer #3: No

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21 Apr 2020

April 20, 2020

Giuseppe Vittorio De Socio, MD, PhD

Academic Editor

PLOS ONE

Dear Dr. Vittorio De Socio:

Re: IMARA: A mother-daughter group randomized controlled trial to reduce sexually transmitted infections in Black/African-American adolescents (PONE-D-19-32194)

Thank you for the opportunity to revise and resubmit for review the above referenced manuscript. We appreciate the very thoughtful and helpful comments from prior reviewers, and we believe that in responding to them, the paper is significantly improved.

In order to address the reviewer’s analytic concerns, we sought the expertise of Dr. Bethany Bray. The original data analyst, Dr. Anna Hotton, was no longer available, and thus, we have updated the authorship list and order to accurately represent the contributions to the manuscript.

Please see each reviewer comment in bold and our response in regular text. Changes in the manuscript are indicated by page and line numbers and they are tracked in the submitted manuscript. We sincerely hope these changes meet with your and the reviewers’ approval.

Please note that we have now included our clinical trial protocol as Supporting Information file.

Sincerely,

Geri R. Donenberg, Ph.D.

Professor of Medicine and Psychology ⏐ University of Illinois at Chicago

Co-Vice Chair of Research ⏐ Department of Medicine

Director ⏐ Healthy Youths Program

Director ⏐ Center for Dissemination and Implementation Science

=========================================================================

Editors Comments and Journal Requirements

i. Please ensure that your manuscript meets PLOS ONE's style requirements, including those for file naming.

We reviewed the manuscript for proper labeling and style requirements.

ii. We note that you have reported significance probabilities of 0 in places. Since p=0 is not strictly possible, please correct this to a more appropriate limit, eg 'p<0.0001'.

We have corrected p = .000 to read p < .001.

iii. … “The information in the registry entry suggests that your trial was registered after patient recruitment began. PLOS ONE strongly encourages authors to register all trials before recruiting the first participant in a study. As per the journal’s editorial policy, please include in the Methods section of your paper”:

iiia) your reasons for your delay in registering this study (after enrolment of participants started);

As now described on p. 6-7, lines 167-195. “This trial is registered at clinicaltrials.gov (NCT02958813). Registration was delayed until 1½ months following the publication of the 2016 Final Policy on the Dissemination of NIH-funded Clinical Trial Information. Up to that point, NIH-funded studies were not required to register, and it was unclear whether the current behavioral study qualified because it did not involve experimental drugs. The Final Rule’s publication expanded and clarified registration requirements, thereby prompting registration.”

iiib) confirmation that all related trials are registered by stating: “The authors confirm that all ongoing and related trials for this drug/intervention are registered”.

This statement has been added to the methods section on p. 6, lines 195-196.

Please also ensure you report the date at which the ethics committee approved the study as well as the complete date range for patient recruitment and follow-up in the Methods section of your manuscript.

The data of ethics committee approval is provided on p. 5, line 167. The complete date range for participant recruitment and follow-up is provided on p. 5, line 123.

iv. We note that you have indicated that data from this study are available upon request. PLOS only allows data to be available upon request if there are legal or ethical restrictions on sharing data publicly.

At the time of original submission, we had not fully de-identified the data or obtained ethics approval to share the dataset. We agree to share a minimal de-identified data set once ethics approval is granted. This will be uploaded as a Supporting Information file.

=========================================================================

Reviewer #1

1. Methods Line 97-99, page 5. Why was the mental health clinic targeted for the initial enrollments? Why this sampling strategy? This may suggest that the study team was more interested in a vulnerable population who definitely may have relational issues with their mothers/caretakers. This could potentially bias the effect of the intervention making it appear positive when it is not. Are you able to describe what mental health problems they had to assure the readers that this would not bias your findings?

We initially targeted youth with mental health problems because we wanted to evaluate the intervention for families likely to have troubled mother-daughter relationships as the intervention was designed to specifically improve mother-daughter relationships. However, as noted by the reviewer, we did not want the intervention to be solely relevant to a vulnerable population, and thus, we opened recruitment to a more generalizable sample to provide a more robust evaluation of IMARA’s efficacy. In fact, only about one-quarter of the girls in the sample met criteria for clinically significant externalizing and internalizing symptoms, respectively, and these rates are similar to general population rates of non-mental health seeking teens. Moreover, the rates did not differ between treatment arms (p > .05). We have added this information to the manuscript to help assure readers that mental health problems would not bias our findings. We also now refer readers to a recent publication from our group that provides an in-depth summary of mental health symptoms in the sample, including testing the effects of IMARA on externalizing and internalizing symptom trajectories over 1 year and the associations of symptom change with future STI acquisition (Kendall et al., in press, Journal of Consulting and Clinical Psychology). Please see p. 14, lines 420-425.

2. Line 113, page 6. What do you mean by dyads learned their group assignment after the baseline assessment....? Make this sentence clear to the reader.

This has been clarified on p. 6, lines 146-149.

3. It is not clear whether the curricular used were hard copies or soft copies on tablets etc. Relatedly, the inclusion criteria ....spoke English.... do the interventions need one to speak English only without reading? Did you do any language proficiency testing for these adolescents?

The curriculum was not delivered through written materials, but rather was conducted by two trained co-facilitators who themselves followed a written manual during in-person face-to-face groups. Being able to read, therefore, was not required to participate. English was an inclusion criterion because the curriculum was conducted in English by the facilitators. We now clarify that the intervention was delivered in English (see p. 7, lines 201 and 204).

4. Line 141. noted rationale for not doing HIV testing but given the strong association between HIV transmission and STIs; at the subset of adolescents that had STIs at 12 months should have received HIV screening. Are the authors able to get this data and include it? may be from a related program etc

We did not have sufficient resources to provide HIV testing to the full sample. However, adolescents who tested positive for a STI and received STI treatment from the study physician were offered HIV testing and partner notification services consistent with Illinois law. Still, these activities were beyond the research protocol, and we did not have participant consent to access this private health information.

5. Line 143-144, page 7. Consistent with Illinois law, expedited partner therapy was offered. Please provide a citation or describe what procedures are done to ensure partner was offered therapy. Also make clear for how long treatment for the STIs was?

STI treatment was offered by the study physician, or youth could opt to receive treatment from their own physician. Where they received treatment from their own physician, we have no information about the partner notification process other than verification via a prescription from the doctor that STI treatment was provided. The standard treatment for all three STIs is single-dose directly observed therapy. We now clarify that STI treatment entailed single-dose directly observed therapy in the revised manuscript (see p. 8, line 221).

6. Line 164. add a citation in support of this information.

Two citations were added to confirm that SISTA and SiHLe contain content that addresses gender and ethnic pride (see p. 9, line 248).

7. Line 165-166, page 8. was this work re acceptability and feasibility published? if yes provide a citation.

This work has not been published.

8. Line 180. Mothers and daughters separately review..... is this referring to the mother and daughter dyad? please make clear

Some of the workshop activities occurred with the mothers as a group separate from daughters, and some of the activities were done with mothers and daughters together in the same group. This is clarified in the text (see p. 9, lines 259-277).

9. Line 203. .... and they did not receive condom skills training. I find this quite surprising in this day and age. Line 205 refers to a 10 minute video demonstrating condom use. How different is the content of this video and the condom skills training? Please clarify

In the IMARA intervention, mothers and daughters were taught the specific steps of condom use and practiced putting a condom on a penis model. They were provided this type of “hands-on” experience with feedback from the facilitators and the group members. By contrast, in the health promotion program, they watched a video that reviewed the steps of condom use, but they did not go through the steps or practice putting a condom on a penis model. This is clarified in the text (see p. 10, lines 296-305).

10. IMARA Fidelity. Noted facilitators rated their adherence to curricular activities. What was fidelity based on the directors report?

All facilitators met initial competency in intervention delivery following the training. Ongoing fidelity was evaluated using facilitator reports of adherence to specific activities. Data are not available regarding adherence as reported by the project director. However, the project director reviewed facilitator reports of adherence following each session and addressed any concerns during weekly meetings. In addition, annual refresher trainings were conducted to prevent facilitator drift from the curriculum. This is now noted in the manuscript (see pp. 11-12, lines 326-331).

Results

11. Did the STI risk differ with type of caregiver?

No, testing positive for an STI at baseline was not significantly associated with type of caregiver. We now report this on p. 14, lines 418-419.

12. Lines 275-279. State the reasons for non-attendance as they may be related to the intervention thus affecting feasibility.

Reasons for non-attendance on day 2 included scheduling conflicts, illness/hospitalization, childcare, and transportation. These are now provided on p. 16, lines 462-463.

13. Describe what STIs were identified at baseline and at 12 months. Do they differ?

We now describe STI frequencies by type (chlamydia, gonorrhea, trichomoniasis) in each arm at each time point (see pp. 14-15, lines 427-440). There were no significant differences between arms in the prevalence of any STI type at any time point (all p-values >.05). However, as noted in the text, the present study was not powered to detect the effects of IMARA on specific types of STIs. Thus, the STI frequencies are provided only for descriptive purposes.

14. Were there any negative outcomes from the intervention e.g caretaker violence, depression, daughter withdrawal etc

In a recent publication now referenced in our manuscript (Kendall et al., Journal of Consulting and Clinical Psychology, in press), we conducted an in-depth analysis of the effects of the intervention on mental health symptoms over 12 months. We found that among girls who entered the study with high versus lower externalizing symptoms, those who received IMARA showed a slightly greater decrease in externalizing scores relative to the control (p = .035). Treatment was not associated with internalizing symptom change (p >.05). The study thus did not provide any evidence of negative mental health outcomes from the intervention.

Two additional factors suggest no negative outcomes related to the study. First, the strong retention rate suggests that dyads felt positive returning for study visits. Second, each mother and daughter separately completed evaluations of the workshop at the end of both days and evaluations were routinely positive; none indicated negative outcomes.

Discussion

15. Line 312. Describe what you mean by advance previous research? may need to reword

Thank you for the opportunity to provide further clarification. We re-worded the sentence as follows: “Findings advance previous research by producing strong effect sizes and treatment effects on biologically determined STIs over 12 months for Black/African-American adolescent girls, who are at elevated risk of STI/HIV relative to White and Latina peers [1, 2].” (see p.17, lines 552-555).

16. Line 314. describe the short term effects and nonbehavioral outcomes. How do they differ from what the IMARA intervention resulted into?

IMARA demonstrated sustained outcomes at 12-months, rather than most studies which report outcomes immediately following an intervention, or at 3- and 6-months follow up. Similarly, “non-behavioral” refers to attitudes and beliefs which may be subject to social desirability bias. These definitions are now added to the sentence (see p. 17, lines 556-557).

17. Line 339. treatment outcomes - clarify which treatment (IMARA or the STI treatment)

We added “IMARA’s positive STI treatment outcomes.” (see p. 19, lines 628-629).

18. Line 360. .... in IMARA were more likely to be tested and treated during the 12 months following intervention. This introduces surveillance bias. Can the authors describe how this bias was overcome as it affects the main study outcome.

It appears the reviewer may have misread the sentence to be that “IMARA girls WERE more likely to be tested and treated.” The statement actually says: “Observed differences in STI rates between groups at one year may suggest girls in IMARA were more likely to be tested and treated during the 12-months following the intervention.”

We do not know if this was the case and have no way to know. Rather, we sought to clarify that if this had occurred and explained the improvement in IMARA STI rates, it would actually provide additional evidence of positive effects of IMARA. However, if this is confusing, we would be happy to delete this sentence.

19. References. Have the citations in brackets as per PLOSONE reference style.

This has been done.

=========================================================================

Reviewer #2

1. Overall. A line or two could be added to describe the potential “mechanisms” by which this intervention might reduce STIs – would it be due to less sex, increased condom use, or lower risk partners?

We added to the statement in the Discussion proposing possible mechanisms related to STI outcomes as follows (see p. 18, lines 601-604): “Finally, IMARA targets individual and social mechanisms shown to affect sexual behavior and these may help explain the reduction in STIs. For example, mental health [3], greater relationship power [4, 5], increased ethnic and gender pride [6], and stronger emotion regulation [7] may influence STI outcomes.”

2. Can the authors include the specific trial number for clinicaltrials.gov?

The trial number, NCT02958813, is now provided (see p. 6, line 167).

3. Could be helpful to understand how much participants were paid to attend the workshops, to help understand its feasibility outside of a research study.

We now clarify the payment for workshops in the Discussion and note it as a limitation with regard to feasibility (see p. 20, lines 664-668): “As with many efficacy trials where participants are compensated to participate in an intervention, this study reimbursed mothers and daughters each $40 to attend each 6-hour workshop day. Providing compensation may limit the feasibility of participation outside the research study, but the small amount – about $7 per hour – was designed to be non-coercive and offset the potential for lost wages.”

4. It would be helpful to know what diagnostic test kit was used to test for chlamydia, gonorrhea and trichomonas (and whether there could be false positives).

For chlamydia and gonorrhea, the name of the test is Abbott Real Time CT/NG assay.

CT sensitivity = 95.2% and specificity = 99.3%

NG sensitivity = 97.5% and specificity = 99.7%

For trichomonas, we used Taq-Man PCR.

Emory Laboratory developed and validated this test and the sensitivity/specificity of the assay is 100% and 99.6% respectively. We would be happy to add this to the manuscript if the reviewer and editor would like.

Results –

5. Can the authors present which specific infections were actually diagnosed – did this intervention reduce chlamydia and gonorrhea and trichomonas? – or was most of the effect related to trichomonas?

Please see our response above to Reviewer 1, Point 14.

6. Were there any questions about self-reported STIs diagnosed outside of the study between baseline and follow-up?

Yes, youth reported at baseline and at 12-month follow-up on whether they had been told by a medical provider that they ever had an STI (at baseline) and over the past 6 months (at baseline and 12 months). We now report these descriptive statistics on p. 15, lines 442-446.

7. Or questions about possible mediators such as self-reported sexual behavior at 12-month follow-up? Or mother-daughter discussions about sexual behavior?

Participants completed a number of survey measures that focused on potential mediators of STIs. However, the primary outcome listed in clinicaltrials.gov was biologically determined STIs. We elected to focus on this outcome given our a priori hypotheses. That said, we do have data on mental health and mother-daughter communication. We have published an analysis of the mental health data, including the associations of mental health symptom change with the protective effect of the intervention against incident STIs (now mentioned in the manuscript; Kendall et al., in press, Journal of Consulting and Clinical Psychology). We plan to examine mother-daughter communication as a mediator of STI treatment effects in the future. Similarly, we have data on self-reported condom use but prefer to report this as a potential mediator after the primary outcome paper is published.

8. It remains a bit unclear what conclusion to make when the unadjusted RR was 0.59 (lower risk), and the adjusted RR was 3.2 (higher risk when comparing to baseline status). This conflicting finding should be discussed more in the discussion. If there was an “a-priori plan” to adjust for baseline STIs included in the clinicaltrials.gov protocol, then the authors should probably be focusing on that result (which showed an increased risk in the intervention group).

Thank you for the opportunity to clarify our writing, which we have done on p. 16. Both RRs were from the same, single model: the first (RR = .57 with 95% CI 0.37-0.88, p=.011) referred to the effect of arm (IMARA vs. health promotion control) on the 12-month STI outcome, and the second (RR = 3.24 with 95% CI 1.78-5.93, p<.001) referred to the effect of baseline STI status on the 12-month STI outcome. We hope it is now clear that there are no conflicting findings, as we are only reporting on the adjusted RR (along with the RR for the covariate), consistent with our a-priori analytic plan.

Minor issues –

9. Methods. the description of the randomization could be more clear how more people were randomized to the intervention – and could refer to the consort diagram (optional – this is presented in the results but could be in the methods).

We have revised the description of randomization and now refer to the CONSORT diagram directly with the hope it is clearer (see p. 6, lines 146-161).

10. Minor – line 246. clarify if the “treatment” refers to the participation in the intervention (or some other sort of treatment…)

We clarify that “treatment” refers to the interventions.

11. Minor – Table 1. more clarify the denominators for the percentages for “sexually active last 6 months and condom use” (mentioned in the footnote, but not obvious when first reading through the table).

We now clarify in the footnote the denominators for the “Sexually active in past 6 months” and “Condom use at last sex” variables. In order to make these notes more obvious when first reading through the table, we now refer to them with an asterisk next to each variable.

=========================================================================

Reviewer #3

Main points

1. Randomisation schedule was created in an unusual way. Dyads were asked to select their randomisation treatment from a paper bag. This could have led to systematic bias and Table 1 indeed shows large imbalances for some of the participants’ characteristics at baseline (e.g. % positive for STI, mean number of STI, ethnicity, history of sex and socio-economic status). These are key common causes of both treatment allocation and incidence of STI so could have confounded the results. Authors should re-perform the analysis after controlling for all these additional imbalanced factors not just for the presence of STI at baseline. Residual confounding should be also mentioned in the limitations (lines 356 onward).

The randomization system was selected for consistency with prior research and theory [8, 9, 10]. It is unclear how participant selection of intervention arm from a paper bag could be related in a biased fashion to other baseline characteristics. All participants had an equal chance of selecting the experimental or control condition.

As stated below in response to Point 6, we agree that the results we presented about differences between arms warrant a more thorough investigation of exchangeability prior to fitting our outcome models. Instead of relying on p-values, we now examine the standardized mean differences between our treatment groups. Based on a general rule of thumb that standardized mean differences above an absolute threshold of .20 may be problematic, we considered all of our standardized differences (which were below .20) to be small, and therefore did not adjust for these variables in subsequent analyses. This is now explained on p. 12, lines 345-350.

2. Similarly, the procedure of alternating between IMARA and the health promotion program would have made the process predictable and broke down the concealment of allocation so that recruiters could have decided not to enrol, say, a problematic dyad if it was known that next allocation would have been for example control and not IMARA.

For every workshop, recruiters scheduled more than 8 dyads with the assumption that randomization would occur. Only the project director knew which arm would be delivered if fewer than 8 dyads arrived for the session. Recruiters were not informed of the decision. Hence, the process was not predictable and concealment of allocation was retained. This is clarified in the text. (see p. 6, lines 154-156).

3. Mothers and daughters in the control arm did not engage in role-plays or joint commune exercises, resulting in lack of blinding. Unclear why efforts were not made to try to implement blinding. This is an additional limitation that should be mentioned in the Discussion.

Families were told they would receive either IMARA or a health promotion program. The health promotion program was very well-received by families as indicated by their post-workshop evaluations. Moreover, we structured the health promotion program to be similar to IMARA in length and amount of time dyads spent jointly and separately. Mothers and daughters actually spent the same amount of time in joint activities, but these were focused on non-sexual health topics (e.g., developing healthy meals and exercise plans). This is now clarified in the text. That said, blinding was not possible because families knew the content of their intervention once they participated. This is now indicated in the limitation section (see pp. 19-20, lines 644-660).

4. Calculation of statistical power is cryptic. It is said that dyads were randomly assigned to the IMARA (n=118) or the health promotion control program (n=81) following an overall ratio of roughly 1.5:1 favouring IMARA to enhance analytic power to detect the treatment effect. Nevertheless, in the Methods power is given for a total sample size of N=200 participants, assuming an even split of 100 vs. 100 in the 2 groups. Authors should show the difference in power using the 1:1 vs. the 1:1.5 random allocation and explicit reasons for choosing the latter. What was the expected increase in power? In general, from the text in lines 251-258, it appears that the sample size of 199 resulted as a consequence of an inevitable attrition between baseline assessment and initiation of the intervention rather than a pre-planned design.

Thank you for highlighting these points. With regard to randomization, we now state the rationale for shifting from 1:1 to 1.5:1 explicitly in the manuscript as follows: “In general, we alternated between IMARA and the health promotion condition, but in the final year of recruitment we favored IMARA to enhance analytic power to detect treatment effects and to provide a large enough sample to evaluate mechanisms associated with key outcomes in IMARA. Although originally unplanned, these strategies led to an overall randomization ratio of approximately 1.5:1 favoring IMARA.” (p. 6, lines 156-160).

With regard to power, the original study design as registered on clinicaltrials.gov was a 1:1 randomization ratio with power calculated according to this assumption. We now explicitly state this when describing randomization on p. 12, lines 336-337. However, in response to the reviewer, we performed calculations to examine the difference in power using a 1:1 vs. 1.5:1 allocation. First we calculated power with a 1:1 allocation using an updated version of G*Power 3.1.9.7, and assuming: (a) a two-sided test, (b) alpha = .05, (c) power = 80%, (d) a relative risk of .40 for IMARA vs. FUEL, (e) STI prevalence in FUEL at follow-up of .25, and (f) equal allocation to IMARA and FUEL. Findings indicated we would need a sample size of approximately 110 participants in each arm. With a sample size of 100 participants in each group [1:1 allocation with 200 total participants], with the same characteristics, the post hoc achieved power is about 76.2%. Of note, the 80% power estimated in the funded grant (and clinicaltrials.gov) in 2009 used an older version of the statistical package. Next, we conducted the same power calculations using a 1.5:1 allocation to IMARA and FUEL, which indicated that we would need a sample size of about 128 participants in IMARA and about 85 participants in FUEL, and if we had a sample size of about 120 participants in IMARA and 80 participants in FUEL [1.5:1 allocation with 200 total participants] then the post hoc achieved power is about 77.7%. The difference between the two power calculations, 76.2% vs. 77.7%, is not substantial.

For the sake of transparency, and because analytic power should not be calculated retrospectively, we retained our original power calculation in the methods section (see p. 12, lines 337-339), but we now state directly that: “Power was not substantially altered when assessed retrospectively for a 1.5:1 allocation favoring IMARA, as was ultimately arrived at in the present study” (p. 12, lines 339-341).

5. Although similar by treatment arm, the rate of non-adherence/loss to follow-up was not negligible at 16% and 10% in the two arms. Because of that it is possible that the two groups are no longer exchangeable at 12 months. It is not an unreasonable assumption in these settings that daughters who are lost to follow-up are more likely to be have acquired STIs. Authors should perform an intention to treat analysis using the missing-failure approach. Alternatively, it is possible that the effect of the strategy could have been diluted by attrition so authors should also perform an on-treatment analysis after controlling for post-baseline confounding factors using a marginal model. This should control for all possible post-baseline prognostic factors as well as common causes of acquiring STI and risk of drop-out.

Thank you for raising these important points; we agree it was an oversight on our part not to have conducted a formal intent-to-treat analysis. We now do so in two ways, as described on pp. 12-13, lines 350-380. First, consistent with the original analytic plan registered at clinicaltrials.gov, we ran the model among only those participants who provided all STI data, and for whom STI status could thus be known at both time points. Second, we conducted a more conservative follow-up intent-to-treat analysis in which participants with missing follow-up data were coded according to their baseline STI status. This approach, also known as the last observation coded forward method, provided a more rigorous check on the original modeling. Both approaches yielded statistically significant support for IMARA. These findings are now described in the results section (pp. 16-17, lines 467-542), and acknowledged in the discussion (p. 17, line 552).

6. Lines 264-273. The issue of baseline exchangeability between arms is ruled out in the Methods with a couple of sentences saying that there was no difference at baseline between the two groups. A p-value >0.05 for these comparisons (line 236) is meaningless and should not be reported as this p-value should be equal to 1 as the null hypothesis is true by definition in a trial. On the other hand, there are larger imbalances between baseline factors which should be described in the text and controlled for in the analysis. For example, mothers in the IMARA arm were less likely to earn <$30k per annum that mothers in the control arm and this could have explained the difference in incidence of STI at 12 months. The sentence that overall >75% (which becomes ‘almost 80%’ in line 351 of Discussion section) of mothers earned <$30k annually in both groups is inaccurate and misleading.

As stated in response to Reviewer 3, Point 1, we agree that the results we presented about differences between arms warrant a more thorough investigation of exchangeability prior to fitting our outcome models. Instead of relying on p-values, we examined the standardized mean differences between our treatment groups. Based on a general rule of thumb that standardized mean differences above an absolute threshold of .20 may be problematic, we considered all of our standardized differences (which were below .20) to be small, and therefore did not adjust for these variables in subsequent analyses. This is now explained on p. 12, lines 345-350.

7. Line 288. This same model adjusted for baseline STI status was RR=3.24, 95% [CI 1.72-6.11], p=.000. Has the direction of RR being inverted? Is this the difference of control vs. IMARA?

Thank you for the opportunity to clarify our writing. The direction of the RR was not inverted. Rather, Both RRs were from the same, single model: the first (RR = .57 with 95% CI 0.37-0.88, p=.011) referred to the effect of arm (IMARA vs. health promotion control) on the 12-month STI outcome, and the second (RR = 3.24 with 95% CI 1.78-5.93, p<.001) referred to the effect of baseline STI status on the 12-month STI outcome. We have clarified this in the manuscript. Please see also our response above to Reviewer 2, Point 8.

8. The fact that the difference observed could be due to mediators is mentioned and several potential mediators are listed e.g. improvements in mother-daughter communication etc. Was use of condom measured in the study? Change in sexual risk behaviour seems to be the most obvious surrogate endpoint/mediator in this analysis to verify.

The observed difference could be explained by a number of potential mediators, but we are reluctant to bring these findings into the current manuscript because they are beyond to scope of the primary outcome paper, consistent with clinicaltrials.gov. We respectfully submit that a subsequent manuscript is warranted where we may thoroughly evaluate mediators of the outcome based on our theoretical framework. Indeed, we recently published a paper on the role of mental health (see Response to Reviewer 2, Point 7 above). We chose to focus this paper solely on the biological outcome rather than self-reported sexual behavior, which is likely subject to greater social desirability or response bias.

9. Line 359. American adolescent girls and their mothers and may not generalise to other groups. Patterns may differ depending on the type of caregiver. For how many dyads the caregiver was not the natural mother? Unclear why a stratified analysis by type of caregiver (mother vs. other) could not be performed.

We did not take this approach both because it was inconsistent with our original analytic plan, and because our study was not powered for such stratified analyses. We now acknowledge this as a direction for future research in the discussion section (see p. 20, lines 662-664).

10. What was the effect of SISTA SiHLE and STYLE compared to this intervention? Results of the various trials should be reported and compared in the Discussion section.

Results from SISTA are reported on p. 4, lines 92-94. Results for SiHLE are reported on p. 4, lines 94-95. Findings from Project STYLE are on p. 4, lines 99-100. We cannot compare the three interventions given significant differences in target populations, research methods, and intervention characteristics. In addition, the study’s primary outcome is not reported for Project STYLE or SISTA. That said, we have strengthened the Discussion to address these issues (see pp. 17-18, lines 559-585).

Other points

1. Lines 248-250. This stringent approach was not intended to be fully powered, but rather to provide a preliminary check of whether the pattern of results observed within the full sample replicated within the subset known to be sexually active at baseline. Indeed, it is very likely to actually be under-powered. Would have been more sensible to restrict the analysis to those who did not show STI at baseline?

In order to address this point, rather than retain the analysis on the sub-sample of youth who were STI-positive at baseline, we instead included in both of the prospective models an interaction term between arm and STI status at baseline. This allowed us to test if there was a significant moderating effect of baseline STI status on the effect of arm (IMARA vs. the health promotion control) on future STI acquisition. As described on p. 13, lines 335-379, the interaction term was non-significant in both models, failing to provide support for significant moderating effects. We thus presented findings from the models without interaction terms, although all models are available upon request. Correspondingly, we removed from Table 1 descriptive statistics on the sub-sample of girls who were STI-positive at baseline and Fig 3.

2. Line 306. Suggested rewording: This study provides preliminary efficacy data indicating that IMARA protects against incident….

The sentence has been re-worded accordingly (see p. 17, lines 544-545).

3. Line 308. The authors claim that for consistency with existing literature past STI occurrence is strongly associated with future acquisition, and so it is standard to co-vary for STI history when predicting future infection. Nevertheless, the unadjusted RR of 0.43 is mentioned here, why?

Please see our response to Reviewer 3, Point 7, above. The 43% risk (corresponding to an RR of .57) indeed represented the adjusted RR. We hope that this point is now clearer within the manuscript.

4. Line 341. Suggested rewording: It is possible THAT girls did not understand the….

If the data are consistent with the literature, why is paragraph (in lines 341-349) needed at all? Or is it instead the case that 33% is likely to be an under-estimate of the prevalence of STI at baseline?

The wording was changed as recommended (see p. 19, line 632)

We opted to retain the paragraph because we believe it is important to (1) report when findings are replicated with previous research, (2) provide interpretations for the inconsistency, (3) underscore the value of biological outcomes relative to self-reports, and (4) underscore the need for future research to find innovative strategies to improve the validity of self-reports. However, we would be happy to remove the paragraph based on the editor’s recommendation.

References

1. Centers for Disease Control and Prevention. HIV Among African Americans 2016 [updated February 4, 2016. Available from: http://www.cdc.gov/hiv/group/racialethnic/africanamericans/index.html.

2. Forhan SE, Gottlieb SL, Sternberg MR, Xu F, Datta SD, McQuillan GM, et al. Prevalence of sexually transmitted infections among female adolescents aged 14 to 19 in the United States. Pediatrics. 2009;124(6):1505-12.

3. Magidson JF, Blashill AJ, Blanco C. Relationship between psychiatric disorders and sexually transmitted diseases in a nationally representative sample. J Psychosom Res. 2014;76(4):322-8.

4. Wingood GM, DiClemente RJ. Application of the theory of gender and power to examine HIV-related exposures, risk factors, and effective interventions for women. Health Educ Behav. 2000;27(5):539-65.

5. Wingood GM, DiClemente RJ. The role of gender relations in HIV prevention research for women. Am J Public Health. 1995;85(4):592.

6. Wilson BDM, Miller RL. Examining Strategies for Culturally Grounded HIV Prevention: A Review. AIDS Educ Prev. 2003;15(2):184-202.

7. Brown LK, Whiteley, L., Houck, C.D., Craker, L.K., Lowery, A., Beausoleil, N., Donenberg, G. The Role of Affect Management for HIV Risk Reduction for Youth in Alternative Schools. . J Am Acad Child Adolesc Psychiatry. 2017.

8. Brown LK, Hadley W, Donenberg GR, DiClemente RJ, Lescano C, Lang DM, et al. Project STYLE: A Multisite RCT for HIV Prevention Among Youths in Mental Health Treatment. Psychiatr Serv. 2014;65(3):338-44.

9. Coleman R. Random Assignment. Designing Experiments for the Social Sciences: How to plan, create, and execute research using experiments. Thousand Oaks, CA: Sage Publishing; 2018. p. 173-210.

10. KP S. An overview of randomization techniques: An unbiased assessment of outcome in clinical research. J Hum Reprod Sci. 2011;4(1):8-11.

Submitted filename: Response to Reviewers.docx

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27 Aug 2020

PONE-D-19-32194R1

IMARA: A mother-daughter group randomized controlled trial to reduce sexually transmitted infections in Black/African-American adolescents

PLOS ONE

Dear Dr. Donenberg,

Thank you for submitting your manuscript to PLOS ONE. After careful consideration, we feel that it has merit but does not fully meet PLOS ONE’s publication criteria as it currently stands. Therefore, we invite you to submit a revised version of the manuscript that addresses the points raised during the review process.

The comments below are minor, but do merit consideration prior to publication.

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We look forward to receiving your revised manuscript.

Kind regards,

Matt A Price

Academic Editor

PLOS ONE

Additional Editor Comments (if provided):

I have a few minor suggestions to consider for this revision.

ABSTRACT: The order of two sentences was a little confusing to me, I initially read the N as the final sample size (ie, taking into consideration loss to follow up). You may wish to reword "Girls provided urine samples to test for N. gonorrhoeae, C. trachomatis, and T. vaginalis infection at baseline and 12-months. Retention at 12-months was 86% with no difference across arms. Mother-daughter dyads were randomly assigned to IMARA (n=118) or a time-matched health promotion control program (n=81)." to something like "Girls provided urine samples to test for N. gonorrhoeae, C. trachomatis, and T. vaginalis infection at baseline and 12-months. Mother-daughter dyads were randomly assigned to IMARA (n=118) or a time-matched health promotion control program (n=81). Retention at 12-months was 86% with no difference across arms."

ABSTRACT: You note that the intent to treat analysis was also significant “albeit with an attenuated magnitude”, yet in your results, the confidence intervals overlap. I suspect your study was not powered to see a difference between a 43% lower chance to contract an STI, and a 37% lower chance. I might change this to read that the ITT was "similar" to your main results, not "attenuated". Those two estimates are statistically very similar (and I would interpret them as essentially the same value).

METHODS: please do add the name of the test kits for CT/NG and TV. You don't need to add the sensitivity and specificity.

DISCUSSION: In the discussion, "STI and HIV" is often mentioned together, yet your study does not test for HIV. You do note this in your response to one of the reviewers, but I think your discussion would benefit with a short mention of this in your 'limitations' paragraph so at least the reader is aware you're thinking of this, even if you weren't able to test for it.

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27 Aug 2020

April 27, 2020

Matthew Price

Academic Editor

PLOS ONE

Dear Dr. Price:

Re: IMARA: A mother-daughter group randomized controlled trial to reduce sexually transmitted infections in Black/African-American adolescents (PONE-D-19-32194R1)

Thank you for the opportunity to revise and resubmit for review the above referenced manuscript. We appreciate the additional helpful comments from the reviewer.

Below, please see the reviewer comments in bold and our responses in regular text. Changes in the manuscript are indicated by page and line numbers and they are tracked in the submitted manuscript. We sincerely hope these changes meet with your and the reviewers’ approval.

Sincerely,

Geri R. Donenberg, Ph.D.

Professor of Medicine and Psychology ⏐ University of Illinois at Chicago

Co-Vice Chair of Research ⏐ Department of Medicine

Director ⏐ Healthy Youths Program

Director ⏐ Center for Dissemination and Implementation Science

=========================================================================

Reviewer Comments

ABSTRACT

The order of two sentences was a little confusing to me. You may wish to reword "Girls provided urine samples…” to something like "Girls provided urine samples to test for N. gonorrhoeae, C. trachomatis, and T. vaginalis infection at baseline and 12-months. Mother-daughter dyads were randomly assigned to IMARA (n=118) or a time-matched health promotion control program (n=81). Retention at 12-months was 86% with no difference across arms."

The reordering of the sentence was done. Please see page 2, lines 33-35.

You note that the intent to treat analysis was also significant “albeit with an attenuated magnitude”, yet in your results, the confidence intervals overlap. I suspect your study was not powered to see a difference between a 43% lower chance to contract an STI, and a 37% lower chance. I might change this to read that the ITT was "similar" to your main results, not "attenuated". Those two estimates are statistically very similar (and I would interpret them as essentially the same value).

We changed to word “attenuated” to “similar”. Please see page 2, line 39.

METHODS

Please do add the name of the test kits for CT/NG and TV. You don't need to add the sensitivity and specificity.

We added the name of the test kits. Please see page 8, lines 163-164.

DISCUSSION

In the discussion, "STI and HIV" is often mentioned together, yet your study does not test for HIV. You do note this in your response to one of the reviewers, but I think your discussion would benefit with a short mention of this in your 'limitations' paragraph so at least the reader is aware you're thinking of this, even if you weren't able to test for it.

We added the following sentences to the limitations section of the manuscript:

“We did not test participants for HIV, because of the low incidence among adolescent girls. However, STIs are a proxy for unprotected sexual activity, a known risk for HIV.”

Please see page 20, lines 441-443.

Submitted filename: Response to Reviewers_R.docx

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11 Sep 2020

IMARA: A mother-daughter group randomized controlled trial to reduce sexually transmitted infections in Black/African-American adolescents

PONE-D-19-32194R2

Dear Dr. Donenberg,

We’re pleased to inform you that your manuscript has been judged scientifically suitable for publication and will be formally accepted for publication once it meets all outstanding technical requirements.

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Matt A Price

Academic Editor

PLOS ONE

Additional Editor Comments (optional):

Reviewers' comments:

22 Oct 2020

PONE-D-19-32194R2

IMARA: A mother-daughter group randomized controlled trial to reduce sexually transmitted infections in Black/African-American adolescents

Dear Dr. Donenberg:

I'm pleased to inform you that your manuscript has been deemed suitable for publication in PLOS ONE. Congratulations! Your manuscript is now with our production department.

If your institution or institutions have a press office, please let them know about your upcoming paper now to help maximize its impact. If they'll be preparing press materials, please inform our press team within the next 48 hours. Your manuscript will remain under strict press embargo until 2 pm Eastern Time on the date of publication. For more information please contact onepress@plos.org.

If we can help with anything else, please email us at plosone@plos.org.

Thank you for submitting your work to PLOS ONE and supporting open access.

Kind regards,

PLOS ONE Editorial Office Staff

on behalf of

Dr. Matt A Price

Academic Editor

PLOS ONE