## Introduction

This paper is concerned with the randomization distributions of ratio statistics and with the means and standard errors of the asymptotic distributions of these ratios and their logarithms. These distributions are important for the correct application and interpretation of this type of statistics, which have found wide use in the analysis and design of randomized weather modification experiments (Adderley and Twomey 1958; Siliceo and Mosino 1963; Kapoor et al. 1973; Dennis et al. 1975; Smith et al. 1979; Changnon 1979; Miller et al. 1979; Gagin and Neumann 1981; Gabriel and Rosenfeld 1990; List et al. 1999). Nowadays it is not difficult to generate a very large number of rerandomizations of an experiment and obtain a reliable estimate of its *P* value without recourse to asymptotic formulas. That approach, however, becomes exorbitant and yields little understanding of the design of an experiment and of alternative methods of analysis. These purposes are better served by application of asymptotic variance formulas to hypothetical models of experiments and will be illustrated in section 5.

Ratio statistics relate totals, or means, of precipitation at different times and in different areas—under cloud seeding or in the absence of seeding, on a seeding target or a control area, or on two alternate targets. The totals cumulate all seeded or unseeded experimental units at all stations of a particular area. Since daily, or even weekly, precipitations tend to have highly skewed distributions, this emphasizes the occasions of extreme precipitation at the expense of the many small or moderate precipitations. Ratio methods may therefore be suspected of being nonrobust and prone to the effect of outliers. Replacing them by statistics that censor outliers, or substitute ranks for amounts of precipitation, would increase robustness but do so at the risk of ignoring the large effects of seeding. Not enough is known about cloud seeding to guarantee that rejecting extreme precipitation events might not result in ignoring its largest effects. Current models of the effect of seeding on precipitation are quite speculative, and so it makes sense to proceed conservatively by analyzing the totals of precipitation, especially as that is what weather modifiers usually aim to affect.

This paper does not argue that ratio statistics are best but presents tools for making correct inferences about them, given that they have been much used and are likely to continue being used.

Two experimental designs are discussed: one has a single target, which is randomly seeded or not seeded;the other uses two targets, which are seeded alternately according to random allocation. Either of these designs may be analyzed with or without covariates. In practice, covariates usually consist of precipitation on nearby control areas that are always unseeded. The targets and controls are assumed to be located so that seeding will affect only the target to which seeding is assigned; in practice, there often are serious concerns about contamination (see, e.g., Wurtele 1971), but these are not addressed here. The units of experimentation are assumed to be well defined at the time of seeding assignment and thus usually consist of fixed time intervals, referred to here as “days.” More meteorologically meaningful units, such as individual clouds, would surely enhance the sensitivity of experiments, but defining them (especially the times of their beginning and end) in real time at the moment of seeding assignment, and/or of finding alternate targets and controls, has proved to be quite elusive. Finally, the length of an experiment, as denoted by the number *n* of days, is assumed to be fixed at the outset of experimentation.

A variety of papers have been concerned with randomization distributions of ratio statistics (Adderley 1961; Moran 1959a,b; Gabriel and Feder 1969; Neumann and Shimbursky 1972; Davis 1979; Petrondas 1983; Gabriel 1988, 1991; Nirel 1994). Other publications have discussed ratio statistics under parametric assumptions (Flueck 1976; Flueck and Holland 1976; Mielke and Flueck 1976; Mielke et al. 1977) and other alternative techniques to avoid normality assumptions (Mielke and Medina 1983).

## Definitions and notation

Consider an experiment carried out on days *i* = 1, . . . , *n* according to random allocation variables *θ*_{1}, . . . , *θ*_{n}, such that, on day *i,* if *θ*_{i} = 1, then one target *Y,* say, is seeded, whereas if *θ*_{i} = 0, then that target is not seeded. In addition, in an alternating targets experiment there is another target *X,* say, which is seeded if *θ*_{i} = 0 and not seeded when *θ*_{i} = 1. The allocation variables *θ*_{1}, . . . , *θ*_{n} are independent, and each has probability ½ for each of *θ*_{i} = 1 and *θ*_{i} = 0.

Precipitations on day *i* are written *y*_{i} and *x*_{i} for targets *Y* and *X,* respectively. Data may also be available on covariates, with *z*_{i,j} denoting the *i*th day’s observation of covariate *Z*_{j}, *j* = 1, . . . , *k,* and a constant is introduced by setting *z̃*_{i,0} ≡ 1 for dummy covariate *Z*_{0}.

In such experiments, the only part that is considered random is the collection *θ*_{i}, . . . , *θ*_{n} of allocation variables, whereas the statistical analysis is conditioned on the observations *y*_{i} and *x*_{i} of precipitation and *z*_{i,j} of covariates, which are taken as given. This approach is particularly useful for testing a hypothesis that observations are independent of allocation, that is, that seeding has no effect on precipitation.

*s̃*

_{Y},

*s̃*

_{X}, and

*s̃*

_{j}are coefficients of variation. Note also that since

*Z*

_{0}has been defined as a dummy covariate, it follows that

*s*

^{2}

_{0}

*s*

_{Y0},

*s*

_{X0}, and

*s*

_{j0}, as well as

*s̃*

^{2}

_{0}

*s̃*

_{Y0},

*s̃*

_{X0}, and

*s̃*

_{j0}, are all zero.

Ratio statistics are calculated from partial sums of precipitation and covariate(s), one sum for days seeded on *Y,* another for days not seeded on *Y.* These sums are obtained by multiplying the summands by *θ*_{i} or 1 − *θ*_{i}, respectively, as shown in Table 1.

## Single target experiments

### The design

An experiment may have a single target *Y,* which is seeded or not seeded according to random allocations *θ*_{1}, . . . , *θ*_{n}, which are independent with Pr(*θ*_{i} = 1) = Pr(*θ*_{i} = 0) = ½, *i* = 1, . . . , *n.* The response is target precipitation *y*_{i} on day *i.* Covariate observations *z*_{i,j}, *j* = 1, . . . , *k* may also be available; they usually consist of precipitation on upwind control areas.

### The single ratio and its approximation

Statistical inferences on seeding effect can be based on the SR_{Y} statistic by relating it to its distribution over all possible random seeding allocations, conditional on the *y*’s. This randomization distribution derives from the randomness of the *θ*’s.

_{Y}can be obtained from the statistic’s logarithm

_{Y}and SR

_{Y}are then found to be asymptotically normal with expectations (E)

_{Y}

_{Y}

_{Y}than for SR

_{Y}.

For experiments with large *n,* one may use these approximate moments for testing significance and setting confidence bounds on the proportional effect of seeding. For intermediate-sized experiments one should preferably use lnSR_{Y} for this purpose rather than SR_{Y} itself. Petrondas (1981) carried out a detailed study of such ratio statistics, noting that “for large datasets . . . Taylor approximation of the variance is adequate. For experiments with fewer than one hundred data points . . . normal approximation is adequate for the central part of the permutation distribution of the logarithm” (of the ratio). He further concluded that “for larger experiments” (over 100 data points) “the normal distribution is adequate” (for the entire permutation distribution).

### The double ratio and its approximation

*z*

_{i,j}on covariates are also available, they may be used to improve the precision of estimating the target’s precipitation by calculating the double ratio (DR)

*a*

_{0},

*a*

_{1}, . . . ,

*a*

_{k}. This compares the SR on

*Y*with a given weighted combination of similar ratios

*Z*

_{1}consisting of precipitation on a control area associated with the target (Adderley and Twomey 1958). For that case,

*a*

_{1}= 1 and

*a*

_{0}=

*a*

_{2}= · · · =

*a*

_{k}= 0), so one may write it DR

_{(0,1)}.

*y*’s and

*z*’s, the randomization distribution of lnDR

_{(a)}, as well as DR

_{(a)}, can then be shown (see the appendix, section b) to be asymptotically normal with expectations

_{(a)}

_{(a)}

_{(0,1)}, this becomes

*a*

_{0},

*a*

_{1}, . . . ,

*a*

_{k}are chosen to minimize the sum of squared residuals

*α*

_{0}and coefficients

*α*

_{1}, . . . ,

*α*

_{k}of the multiple regression of the differences

*ỹ*

_{i}− 1 onto the covariates

*z̃*

_{i,j}− 1,

*j*= 1, . . . ,

*k,*all relative to their means. In particular,

*α*

_{0}= 0 since both the

*ỹ*

_{i}− 1 and the

*z̃*

_{i,j}− 1,

*j*= 1, . . . ,

*k,*sum to zero. The resulting statistic is the regression ratio (RR):

*y*’s and

*z*’s, to be asymptotically normal with expectationsand variances

*R*

^{2}

_{Y:1,...,k}

*ỹ*

_{i}− 1 onto the covariates

*z̃*

_{i,j}− 1,

*j*= 1, . . . ,

*k.*

Note that the fit, and the correlation, of the above regression is the same as that of the regression of the precipitation *y*_{i} onto the covariates *z*_{i,j} themselves (not relative). Hence, one could use the latter multiple regression instead of the former to obtain the same result.

## Alternating targets experiments

### The design

An experiment may have targets *Y* and *X,* which are seeded on alternate days where the alternation is according to random allocation *θ*_{1}, . . . , *θ*_{n}, which are independent with Pr(*θ*_{i} = 1) = Pr(*θ*_{i} = 0) = ½, *i* = 1, . . . , *n.* The responses are precipitation *y*_{i} and *x*_{i} on alternate targets *Y* and *X* on day *i.* Covariate observations *z*_{i,j}, *j* = 1, . . . , *k* may also be available. The covariates usually are precipitations on several control areas, some upwind of target *Y,* others upwind of target *X.*

### The root double ratio and its approximation

_{Y}and/or the reciprocal of the analogous single ratio

*X*precipitation. Note that a positive effect of seeding would increase the reciprocal of SR

_{X}, not SR

_{X}itself. This is because in the alternating targets experiment

*X*is seeded when

*θ*

_{i}= 0 and is not seeded when

*θ*

_{i}= 1. A summary statistic for evaluating the overall effect of seeding on the two targets therefore has to average SR

_{Y}and 1/SR

_{X}. This is done by the root double ratio (RDR; Moran 1959a,b):

_{Y}and 1/SR

_{X}.

Comparing this with the single area experiment’s DR_{(0,1)}, one notes it differs by introducing the square root. This is justified because DR_{(0,1)} compares SR_{Y} to the SR_{1} for control *Z*_{1}, which could not be affected by seeding, whereas RDR compares SR_{Y} to SR_{X} for the alternate target *X,* which could be reciprocally affected by seeding; the square root then averages over the effects on the two targets.

*x*’s and

*y*’s. Asymptotically, lnRDR and RDR are, conditional on the

*x*’s and

*y*’s, asymptotically normal withand

### The root quadruple ratio and its approximation

*z*

_{i,j}on concomitant variables

*Z*

_{j},

*j*= 1, . . . ,

*k*are available, one may use them to adjust the comparison of the two targets’ precipitation by calculating the root quadruple ratio (RQR):

*b*

_{0},

*b*

_{1}, . . . ,

*b*

_{k}. This compares the RDR, which is the square root of SR

_{Y}divided by SR

_{X}, with the square root given weighted combinations of single ratios

_{Zj}

*j*= 0, 1, . . . ,

*k.*For suitable covariates that may improve the precision of the estimate of the proportional seeding effect. The RQR was originally used for a pair of covariates

*Z*

_{1},

*Z*

_{2}, which represented precipitation on control areas upwind of targets

*Y*and

*X,*respectively. For that case,

*b*

_{1}= 1,

*b*

_{2}= −1 and

*b*

_{0}=

*b*

_{3}= · · · =

*b*

_{k}= 0 and the statistic becomes RQR

_{(0,1,−1)}(Gabriel and Rosenfeld 1990).

*y*’s,

*x*’s, and

*z*’s, the randomization distribution of lnRQR

_{(b)}, as well as of RQR

_{(b)}, is shown (see the appendix, section e) to be asymptotically normal with expectations

_{(b)}

_{(b)}

### The root regression ratio and its approximation

*b*

_{0},

*b*

_{1}, . . . ,

*b*

_{k}of the RQR are chosen to minimize the sum of squared residuals Σ [

*ỹ*

_{i}−

*x̃*

_{i}− Σ

_{j}

*b*

_{j}(

*z̃*

_{i,j}− 1)]

^{2}, they become the intercept

*β*

_{0}= 0 and coefficients

*β*

_{1}, . . . ,

*β*

_{k}of the multiple regression of the differences

*ỹ*

_{i}−

*x̃*

_{i}onto the concomitants

*z̃*

_{i,j},

*j*= 1, . . . ,

*k,*all relative to their means. The resulting statistic is the root regression ratio (RRR)

*β*

_{1}, . . . ,

*β*

_{k}are the intercept and coefficients of the regression of the differences

*ỹ*

_{i}−

*x̃*

_{i}onto the concomitants

*z̃*

_{i,j},

*j*= 1, . . . ,

*k,*all relative to their means.

*R*

^{2}

_{Y−X:1,...,k}

*ỹ*

_{i}−

*x̃*

_{i}) with the covariates

*z̃*

_{i,j}− 1,

*j*= 1, . . . ,

*k.*

Note that the fit and the correlation of the above regression is the same as that of the regression of the difference of the targets’ relative precipitation *ỹ*_{i} − *x̃*_{i} onto the covariates *z*_{i,j} themselves (not relative). Hence, one could use the latter multiple regression instead of the former to obtain the same result.

## A schematic comparison of designs and ratio statistics

### The schema

The formulas developed in the preceding sections allow calculation of the variances of different ratios when the relative variances and covariances of all variables are known. Given, however, that certain common patterns have been observed in many precipitation experiments, we propose a schema of variances and correlations that roughly represent observed patterns. We then derive the ratios’ variances from this schema and make some fairly general comparisons of various ratio statistics in terms of their variances and thus in terms of the length of experimentation they require.

The schema, Fig. 1, concerns one or two targets, *Y* or *Y* and *X,* with corresponding control(s) *Z*_{1}, or *Z*_{1} and *Z*_{2}, respectively. (Illustrations follow in Tables 2 and 3 below.) It thus includes both one- and two-target designs. It assumes the relative variances of all variables are the same, that is, *s̃*^{2}_{Y}*s̃*^{2}_{X}*s̃*^{2}_{1}*s̃*^{2}_{2}*σ̃*^{2}*r*_{Y1} = *r*_{X2} (=*κ,* say). Also, the correlation of each target with the other’s control is assumed to be the same for both targets, *r*_{Y2} = *r*_{X1} (=*γ,* say). And finally, the correlation between the targets is assumed to be the same as that between the controls, *r*_{YX} = *r*_{12} (=*τ,* say). These are not unreasonable approximations to observed patterns, and they lead to an *κ* ≥ *τ* ≥ *γ* ≥ 0 order since controls are chosen to be as highly correlated with their targets as possible, more so than alternating targets are to each other. The cross correlation of each target to the other’s control is obviously least.

### Some examples

Examples of alternating targets experiments with controls are Israel II (Gagin and Neumann 1981; Gabriel and Rosenfeld 1990) and Puglia (List et al. 1999) with the correlations and coefficients of variation as shown in Table 2.

For the Israeli data, the coefficient of variation is remarkably constant at around 1.25. The target–control correlation average is 0.753, whereas the between-target and between-control correlation average is 0.738, which is a bit lower, as postulated under the schema. The lowest are the target–other control correlations, which average 0.665, again as expected. The two correlations of each kind do not closely correspond to the schema, that is, 0.866 is not close to 0.641, 0.668 to 0.808, and 0.745 to 0.584, so the approximation to the Israeli situation is rough.

For the Puglia data, Table 3, the coefficient of variation is fairly steady around 1.60. The target–control correlation average is 0.832, the between-target and between-control correlation average is 0.508, which is a bit lower than postulated under the schema. Least is the target–other control correlation with an average of 0.498, again as expected. Again, the two correlations of each kind are not very close together, so the schema is likely to be a rough approximation of the Puglia situation.

Relative variability, that is, the coefficient of variation, is somewhat higher in Puglia than in Israel; however, once adjusted for the control covariate, it does not vary widely, which suggests that important features of experiments in these two areas may not be that different.

### Some comparisons and practical conclusions

The variances of the various ratios for single and alternating targets experiments are shown in Fig. 2, both as derived generally in sections 3 and 4, and as calculated under the simplified schema.

In a single target experiment the double ratio DR_{(0,1)} is seen to be more precise, that is, to have smaller variance than the single ratio SR_{Y}, provided the target–control correlation *κ* exceeds 0.5. The table also shows RR to be the more precise than either, so it should always be used, unless no suitable control is available and only SR_{Y} is available.

In an alternating targets experiment the root quadruple ratio RQR_{(0,1,−1)} is similarly seen to be more precise than the root double ratio RDR, provided *R*_{Y−X:1,2} = (*κ* − *γ*)/(1 − *τ*) exceeds 0.5. The RRR is, however, found to be the most precise and should always be used if controls are available; in the absence of controls, only the RDR is available.

Comparing an alternating targets experiment with a single target experiment, both without controls, the former’s RDR will have a smaller variance, (1/*n*)*σ̃*^{2}2(1 − *τ*)_{Y}, which has variance (4/*n*)*σ̃*^{2}*τ*)/2 of the latter, so it will need less than half as many observations for the same precision. The advantage of the alternating targets design evidently gets more pronounced as the correlation *τ* between the targets increases.

*R*

^{2}

_{Y−X:1,2}

*κ*−

*γ*)/(1 −

*τ*))

^{2}of

*Y–X*onto

*Z*

_{1}and

*Z*

_{2}, which is particularly large if the correlation

*κ*of each target with its control is much larger than its correlation

*γ*with the other control.

## Additional issues

### Power and length of experimentation

The above expressions for the expectations and variances of ratio statistics have been computed under the null hypothesis that seeding has no effect and are conditional on the first two moments of target precipitation and the covariates. They can be used to assess the powers of planned experiments and the length of experimentation needed for a given power.

For any ratio statistic *R,* if seeding were to increase the precipitation every day by a proportion *δ,* this would add ln(1 + *δ*) to ln*R.* The expectation of ln*R* would increase by ln(1 + *δ*), whereas the variance would remain the same. Standard formulas for power can therefore be applied provided one has estimates of the relative variation of precipitation and the covariates.

*R,*the variance can be written Var[ln

*R*] ≈ (1/

*n*)

*ψ*

^{2}

_{R}

*ψ*

_{R}, see Fig. 2. From standard statistical methodology, the power of an experiment at significance level

*α*which lasts

*n*days then is

*z*

_{α}is the

*α*th quantile of the standard normal distribution. Conversely, a power of 1 −

*β*at level

*α*is attained by an experiment whose number of days is

*ψ*

_{SRY}

*s̃*

^{2}

_{Y}

*n*days is

*β*at level

*α*is attained by an experiment whose number of days is

*s̃*

_{Y}= 1.447, 90% power (

*β*= 0.10, so

*z*

_{β}= 1.28), to discover a 15% (

*δ*= 0.15) increase of precipitation at a significance level of 5% (

*α*= 0.05, so

*z*

_{α}= 1.645) would have required some

_{Y}rather than of lnSR

_{Y}that is used here. It is not completely clear whether the latter is preferable for calculating power.]

*ψ*

_{RRR}= (

*s̃*

^{2}

_{Y}

*s̃*

_{YX}+

*s̃*

^{2}

_{X}

*R*

^{2}

_{Y−X:1,...,k}

*n*days’ length is

*β*at level

*α*is attained by an experiment whose number of days is

*s̃*

^{2}

_{Y}

*r*

_{YX}

*s̃*

_{Y}

*s̃*

_{X}+

*s̃*

^{2}

_{X}

^{2}− 2(0.6073)(1.447)(1.631) + (1.631)

^{2}= 1.8874, and

*R*

^{2}

_{Y−X:1,2}

### Comparisons of different experimental designs

*Y*experiment that is to be evaluated by DR

_{(0,1)}relative to a control area

*Z*

_{1}=

*X.*Compare this with an alternating

*Y*and

*X*target experiment to be evaluated by RDR. From Fig. 2,

*Z*

_{1}=

*X,*and thus

*κ*=

*τ,*these expressions differ only by a factor of 4 and the single target experiment would need four times as many days as the alternating targets experiment to achieve the same power.

Actual experiments commonly have controls that are more highly correlated with a target than with an alternate target, that is, *κ* > *τ,* so the ratio of Var[lnRDR] to Var[lnDR_{(0,1)}] is larger than 0.25. For the Bari target in the Puglia experiment, *τ* = 0.61 and *κ* = 0.77 and so the variance of the alternating targets experiment’s RDR would have been 0.42 of the variance of a single target experiment’s DR_{(0,1)}.

### Some general comparisons

*β*at level

*α*would be

_{Y}and

Taking rough average values from the Israeli II and Puglia experiments, we would put *κ* = 0.8, *τ* = 0.65, and *γ* = 0.6, and coefficients of variation *σ̃**σ̃*

The data from both experimental regions show that single area experiments on days are impractical; certainly so if there is no control and in practice also in the presence of a control, since it is not realistic to design experiments of 15–20 years’ duration. The data from both experiments also show that alternating targets experiments require some 5–6 years for reasonable power if a 15% seeding effect is tested for and that the use of control covariates does not significantly reduce the time requirement. In the author’s experience, those seem to be the order of magnitude for experiments of this type in general.

Single area experiments could therefore be viable only with some drastic change from the designs studied above. Thus, better covariates might be helpful if they can be found, as would better focused experimental units that reduced variability, and, of course, seeding techniques that justified testing for bigger effects than the ones hoped for from AgI seeding. Without any of these, alternate targeting is the only game in town.

## Acknowledgments

Dr. B. A. Silverman’s generous advice and critical encouragement of the formulation of this paper are greatly appreciated.

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## APPENDIX

### Asymptotic Randomization Distributions of Ratio Statistics

#### Single ratio SR_{Y}

*y*

_{i}

*θ*

_{i}= Σ

*y*

_{i}/2 and the last two about Σ

*θ*

_{i}=

*n*/2. The resulting first-order approximation is

*θ*’s are independent, each with expectation ½ and variance ¼, it follows from the central limit theorem (see Gabriel and Feder 1969) that, conditional on the

*y*’s, the distribution of lnSR

_{Y}is asymptotically normal. The same is true of the distribution of SR

_{Y}since SR

_{Y}≈ 1 + lnSR

_{Y}when SR

_{Y}is near 1, but its convergence is slower. The expectations are readily worked out to be

*E*

_{Y}

*E*

_{Y}

#### Double ratio DR_{(a)}

*y*’

*s*and

*z*’

*s,*the randomization distributions of lnDR

_{(a)}and DR

_{(a)}are asymptotically normal with expectations

_{(a)}

_{(a)}

#### Regression ratio RR

*a*

_{0},

*a*

_{1}, . . . ,

*a*

_{k}of the double ratio DR

_{(a)}are chosen to minimize the sum of squared residuals Σ (

*ỹ*

_{i}− 1 − Σ

_{j}

*a*

_{j}(

*z̃*

_{i, j}− 1))

^{2}so that

*R*

^{2}

_{Y:1,...,k}

*ỹ*

_{i}− 1’s on the

*z̃*

_{i,j}− 1’s.

#### Root double ratio RDR

*θ*is replaced by its expectation ½. Thus, the first two terms are expanded about Σ

*y*

_{i}

*θ*

_{i}= Σ

*y*

_{i}/2 and the last two are expanded about Σ

*x*

_{i}

*θ*

_{i}= Σ

*x*

_{i}/2. The resulting first-order Taylor approximation is

*θ*’s are independent, each with expectation ½ and variance ¼, it follows that, conditional on the

*x*’s and

*y*’s, lnRDR and RDR are asymptotically normal withand

#### Root quadruple ratio RQR_{(b)}

*y*’s,

*x*’s, and

*z*’s, the randomization distributions of lnRQR

_{(b)}, and RQR

_{(b)}, are asymptotically normal with expectations

_{(b)}

_{(b)}

#### Root regression ratio RRR

_{(b)}by choosing the coefficients

*b*

_{0},

*b*

_{1}, . . . ,

*b*

_{k}so as to minimize the sum of squared residuals Σ [

*ỹ*

_{i}−

*x̃*

_{i}− Σ

_{j}

*b*

_{j}(

*z̃*

_{i,j}− 1)]

^{2}. This sum then becomes Σ (

*ỹ*

_{i}−

*x̃*

_{i})

^{2}(1 −

*R*

^{2}

_{Y−X:1,2,...,k}

*y*’s,

*x*’s, and

*z*’s, the randomization distributions of lnRRR and RRR are asymptotically normal with expectationsand variances

Variances of different ratio statistics, general and schematic.

Citation: Journal of Applied Meteorology 38, 3; 10.1175/1520-0450(1999)038<0290:RSFREI>2.0.CO;2

Variances of different ratio statistics, general and schematic.

Citation: Journal of Applied Meteorology 38, 3; 10.1175/1520-0450(1999)038<0290:RSFREI>2.0.CO;2

Variances of different ratio statistics, general and schematic.

Citation: Journal of Applied Meteorology 38, 3; 10.1175/1520-0450(1999)038<0290:RSFREI>2.0.CO;2

Totals and means for single target and alternating targets experiments. Note that Σ without an index will be considered to have index *i* running from 1 to *n.*

Coefficients of variation and correlations of targets and controls for the Israel II experiment. (The corresponding parameters from the model of Fig. 1 are indicated as approximations.)

Coefficients of variation and correlations of targets and controls for the Puglia experiment. (The corresponding parameters from the model of Fig. 1 are indicated as approximations.)

Number of days (years) needed for different designs and statistics to yield 90% power of detecting a 15% increase with 5% significance; approximations under schematic assumptions for the Israel II and Puglia experiments.