Title: Modelling timing of sexual debut among women in Zimbabwe using a Geoadditive
Discrete- Time Survival approach
Version: 0 Date: 22 Mar 2024
Reviewer's report:
This paper aims to assess the determinants of early sexual debut in Zimbabwean women,
considering both socio-economic and demographic factors and regional variation. The results are
consistent with most previous studies, showing that early sexual debut appears to be associated
with low educational attainment and lower family wealth. However, this is difficult to interpret,
as association does not necessarily imply causation, especially when the temporal ordering of
the outcome and the exposure are unclear. The paper is mostly clear, but the mathematical
presentation of the methods needs some work.
Major comments
Although the authors acknowledge that there may be biases in self-reported data on age at
first sex, they don’t include much discussion/analysis on how this might affect the results. For
example, the study by Nguyen and Eaton (reference number 19) found that younger women
tend to report a later age at sexual debut than when interviewed at later ages. How does this
affect the interpretation of the birth cohort ‘effects’ that the authors have identified? Nguyen and
Eaton estimated that in Zimbabwe the trend was towards LATER age at sexual debut in recent
generations (after accounting for reporting biases), which is the opposite of what the present
study is suggesting. Can the authors talk about why their findings are different?
There are some quite serious problems with the equations and statistical definitions in this paper.
For example, in the last paragraph of page 9, the definition of T is unclear. When you say “time
to early sexual debut”, you mean time after age 8 (i.e. 9 years is the minimum)? And if the
maximum value is 10, how is T defined for a woman with a sexual debut after age 18? Similarly,
when defining ti (after equation 2) it would be more correct to define it as the earlier of age at
first sex, the age at the time of the survey, and age 18 (in all cases, subtracting 8). Only in the
first of the 3 cases would #i be set to 1 (I'm using # here in place of "lower case delta", because
this reviewer system doesn't seem to support Greek lower case). The authors say that women
with non-early sexual debut had “either age at first sexual encounter or interview used for ti”,
but this doesn’t make sense if T is being defined as the set with maximum value of 10 and ti
is an element of T. I’ve included more detailed comments on the statistical presentation in the
“minor comments” below, but I would urge the authors to make sure that the presentation of the
statistical methods is carefully checked by an expert statistician before re-submitting.
I’m not sure that it makes sense to control for marital status in these models. Marriage would
almost always follow sexual debut or occur at the same age as sexual debut, so it shouldn’t be
considered a predictor of sexual debut.
It’s confusing that the authors refer to time-updated covariates early in the paper, but in equation
4 it seems they’re only considering fixed covariates (?). This is particularly important for the
education variable, because a woman’s education at the time of sexual debut might be very
different from her education at the time of interview. The education coefficients are hard to
interpret if they’re not time-updated (see my earlier comment about the difficulty of inferring
causation, particularly when the ordering of event and exposure is uncertain). Early sexual debut
is strongly associated with teenage pregnancy, which in turn is associated with school dropout,
so low educational attainment could well be the consequence of early sexual debut rather than
the cause.
Minor comments
Last paragraph of p. 5: The first sentence is unreferenced and seems almost biologically
implausible – it also seems dangerous to make policy recommendations based on isolated cases.
This sentence could be cut. In the same paragraph the authors refer to “the abundance of cases
of underage pregnancy”, but without citing any evidence to show this.
Last paragraph on page 7: The sentence “A sample of 11,196 households was involved in
the survey” seems to be out of place – it should be removed (and indeed it gets repeated in
the following paragraph, where it’s more appropriate). Also, it’s not necessary to list the 10
provinces.
Last paragraph of page 8: There is some unnecessary repetition of the motivation for discrete
time models that was given in the introduction.
Equation 2: The indexing is incorrect. The indexing in the multiplication term should be with
respect to s and not t (and t should be the upper limit, not s).
First paragraph, page 11: The authors use the same symbol to represent the spatially correlated
and uncorrelated terms.
Equation 6: The definition of g_spat should be conditional on {g_spat(l); l#s}, not a single value
of g_spat (l). Also in the same equation the authors have l##s, which should be l#Ds, where Ds
represents the set of districts neighbouring s. Note that you should NOT use # to represent the
set, because it was already defined earlier to represent the censoring indicator.
First paragraph of page 12: The authors refer to 4 different models, but the descriptions of
the 2nd and 3rd are the same. Also it’s not quite clear what they mean by “convolutional
model” (presumably they mean the full model?).
In the same para the authors refer to a burn-in of 200, which sounds very short.
First paragraph of Results: The authors say that Bulawayo had the lowest prevalence of ESI
(25%), but this looks inconsistent with the shading on the graph (which suggests lowest
prevalence in the southeastern districts).
Table 2: What is the purpose of the A-D footnotes if they’re just repeating the column headings?
I struggled to interpret some of the results in Table 2. In particular, how are the “random effects”
supposed to be interpreted? Also, when presenting the statistical methods earlier, the authors
made several references to non-linear terms, but these aren’t clear from the results presented
(the model seems to be showing only linear terms?).
Page 19, 1st paragraph: Here the authors refer repeatedly to “first sex” as the outcome, when it
should rather be “early sexual debut”.
Figure 3: I would change the x axis to start at 8 (not 1), otherwise it’s incorrect to label this as
age at sexual debut. Also I don’t understand why the authors are showing the hazard beyond
10 (age 18) since they said the disregarded data on sexual debut after age 19 when fitting the
model (?). Lastly, I would make it clear in the y axis label or in a footnote that this on a log
odds scale. (As an aside, one could potentially drop Figure 3, as it’s not critical to the overall
understanding of the paper.)
Figure 4 labels: Change to left, centre and right in the figure title (when referring to the three
different panels). Why is the colour shading inconsistent across the three panels? If you had used
a consistent shading, it would have been clear that the structured spatial model implies much
less variation in rates of sexual debut than the other 2 models.
Page 24, 2nd paragraph: There are lots of grammatical errors/typos here.
Page 24, last paragraph: Explaining Matabeleland North’s high rates of sexual debut in terms of
limited education doesn’t make sense because the authors are already controlling for education
in the statistical model (?).
Page 25, 2nd paragraph: The recommendation to target Muslims and women with other religions
is perhaps inappropriate, given that (as the authors acknowledge) the numbers are too small to
differentiate between these different religious groupings.
The conclusion section repeats a lot of what was previously said in the discussion, and is too long
(currently four paragraphs, where it would be more conventional to have a single Conclusions
paragraph). Strengths and limitations wouldn’t conventionally be included in the conclusions
section, and should rather be in the discussion.
Recall bias should also be listed as a limitation.