Progesterone to Prevent Recurrent Preterm Delivery – How Much Do We Know? (Part 2)
Scroll down to the bottom of this post for the essentials.
Soon after the da Fonseca trial (Part 1) appeared in the literature, the New England Journal of Medicine published a large randomized clinical trial examining weekly intramuscular injections of 17 alpha-hydroxyprogesterone caproate (17-OHPC) to prevent recurrent preterm delivery. The results of this trial led to FDA approval of 17-OHPC for this purpose conditional upon the conduct of another, confirmatory trial (recently completed).
The trial. The “Meis trial,” as it is known, was sponsored by the National Institute of Child Health and Human Development and involved many academic medical centers from around the United States. Noting that two meta-analyses had been done to summarize the findings of smaller trials examining the use of progesterone to prevent preterm delivery, they noted that the one which focused on 17-OHPC found it to be effective while the one assessing “progestational compounds” did not. Therefore, they chose to use 17-OHPC, described as a natural metabolite of progesterone. The primary objective was to determine if 17-OHPC can reduce the likelihood of preterm delivery in a current pregnancy among women who have had a previous preterm delivery (delivery at <37 weeks of gestation).
Women had to be at least 15 weeks and no more than 20 weeks 3 days of gestation at enrollment, have a documented history of preterm delivery of a liveborn singleton infant due to spontaneous preterm labor or rupture of membranes. If the current pregnancy involved >1 fetus, a planned cervical cerclage (procedure involving stitches or tape to try to keep the cervix closed), or the current fetus had a known congenital anomaly, in addition to some other exclusion criteria, the woman could not be enrolled.
Urn randomization was used to assign the women to weekly intramuscular injections of either 17-OHPC or placebo (castor oil – since the 17-OHPC medium was castor oil). What the heck is “urn” randomization? This is a form of adaptive randomization, meaning that subsequent women’s chances of being randomized to 17-OHPC or placebo partially depends on which groups previous women have been assigned to. This might sound odd but is a valid method. It serves two purposes. The first is to ensure that both study groups have the intended numbers of women in them. Particularly with respect to smaller trials (e.g., <200 participants), simple randomization may not produce a 50%/50% (or close) split between experimental and control groups. This reduces the statistical power of the trial, or the chance that it will find that experimental and control groups are different in terms of the primary outcome – if there really is a difference.
Its second purpose is to foil clever clinicians who know that with block randomization, the assignment of a subset of patients will be known ahead of time, allowing them to decide what study groups patients get into. (We’ll save block randomization for another post.) Hiding the treatment assignments produced by randomization is known as “allocation concealment.” If you can line up patients according to the randomization list, you’ve defeated the purpose of randomization.
The way urn randomization works is roughly as follows: it tracks the proportion of patients in each study group as enrollment takes place. If the proportions get too far away from 50%/50% (or whatever the percentages should be), it adjusts the treatment assignment percentages so that the group with too few patients has a slightly higher chance of getting the next patient. Or, it may even be employed continually so that if a patient gets assigned to the control group, the assignment probabilities for the next patient will be very slightly weighted towards getting the experimental treatment, and vice versa.
Anyway, the patients in the Meis trial were randomized to their weekly intramuscular injections and followed until they delivered their babies. Except for the injections, their care was not dictated by the protocol. The investigators accumulated 310 women in the 17-OHPC group and 153 women in the placebo group (the randomization was 2:1 for 17-OHPC vs. placebo). Compliance was very high at 91.5% of patients coming in for all of their injections on schedule (they couldn’t go >10 days between injections).
The characteristics of the women in the 17-OHPC and placebo groups were similar as expected, with one glaring exception. Forty-one percent (41.2%) of women in the placebo group had a history of >1 preterm delivery vs. 27.7% for women receiving 17-OHPC. That is a huge imbalance in a large trial of 463 women. Having more than one previous preterm delivery further increases your risk of the current pregnancy resulting in a preterm delivery, so if the placebo group had a higher preterm delivery rate it could be due to this factor rather than due to the 17-OHPC being effective at preventing preterm delivery. It’s not what you want in your trial at all.
Based on data the investigators had from another large study in a similar population of women, they were expecting a preterm delivery rate of 37% in the placebo group, with a reduction to 25% in the 17-OHPC group. What they actually saw was a 55% rate in the placebo group and 36% rate in the 17-OHPC group. This is a problematic outcome. What you want in a control group is “boring.” You want characteristics that are typical, and outcomes close to expected. That’s the standard against which you’re trying to compare the new (experimental) treatment. If you’re comparing the experimental group’s outcome to something unusual, what does it mean?
The 17-OHPC group’s preterm delivery rate was very close to the 37% expected for the control group. The explanation given is that “the women in this trial were very high risk women.” Okay … except the placebo group women were more likely to have had >1 previous preterm delivery – we know that group were very high risk! I’m not sure about the 17-OHPC group women. The investigators did an unnamed analysis to control for the higher rate of >1 preterm delivery in the placebo group, and said it didn’t change their overall conclusion (it reduced the difference between groups by only a small amount). That is, they did this for the preterm delivery rate at <37 weeks, but did not report it for <35 and <32 weeks (two other outcomes they reported).
An FDA review of the Meis trial showed that the risk of preterm delivery was decreased in the 17-OHPC group whether they had a history of one, two, or three or more preterm deliveries, supporting the idea that 17-OHPC prevents preterm delivery.
There are a couple of other results reported in the trial which I consider somewhat incongruous under the assumption that 17-OHPC reduces spontaneous preterm delivery. The 17-OHPC placebo groups were similar with respect to the frequency of hospital visits for preterm labor and use of tocolytic drugs. (Tocolytic drugs are given to try to stop preterm uterine contractions.) It seems like a group who ended up with a higher preterm delivery rate would be more likely to show up at the hospital with preterm contractions and be given drugs to stop the contractions? I assume the hospital visits for preterm labor were visits that did not end up in delivery.
So the quality of evidence from this trial is mixed. A large imbalance in a key risk factor was seen between the 17-OHPC and placebo groups, and this is highly unlikely when randomizing a large number of patients (but not impossible). The control group had an unexpectedly high rate of preterm delivery while the 17-OHPC group had almost exactly the rate expected if they had been given placebo. However, analysis of subgroups based on history of one, two or ≥3 preterm deliveries was consistently in favor of 17-OHPC.
The Essentials
| Concept or Issue | Description | Why It’s Important |
| Urn Randomization | Random assignment to study group of later participants is partly based on the assignment received by previously-enrolled participants. This is done to achieve the intended proportion of participants in each study group (e.g., 50% control and 50% experimental). | Simple randomization does not guarantee that the intended proportion of participants assigned to each group will occur, especially in smaller trials (e.g., the trial ends up with 40% control and 60% experimental). This reduces the statistical power of the trial to identify a difference between control and experimental if that is the true state. It also eliminates a potential problem with block randomization which can reveal the next treatment assignment for a subset of participants. |
| Allocation Concealment | In randomized trials, this is preventing people involved in conducting the trial from knowing the sequence of treatment assignments produced by randomization. In other words, when a participant is enrolled it is not known what treatment they will be assigned to. | When investigators and others know the randomization schedule (sequence of treatment assignments), they can subvert the process and negate the benefits of randomization. They can select which patients get into a particular study group, essentially “unrandomizing” the trial and causing groups not to be equivalent on important characteristics. There are documented instances of this. |
References
Meis PJ, Klebanoff M, Thom E, Dombrowski MP, Sibai B, Moawad AH, et al. Prevention of recurrent preterm delivery by 17 alpha-hydroxyprogesterone caproate. NEJM 2003 Jun 12;348(24):2379-2385.
U.S. Food and Drug Administration. FDA Briefing Document NDA 021945 Hydroxyprogesterone Caproate Injection. Available at: https://www.fda.gov/media/132003/download. Accessed 1/19/2020.