Since each time you had two groups and mutant was normalized against control so paired test can be preformed. The issue will be whether the fold changes can fit t-distribution or not. If there did then paired t-test can be used. If not you can try logrithm transformation then do oaired t-ttest. Another method is to do paired non-parametric test. However, since then control is always 1 so most software will not process it. Hope this can help you.

First make sure your repeats are from different extractions. That being said, also make sure that the exposure time is the same (relatively) for all repeats. Saturation may highly influence your read and affect variability. As for the statistics, I think a paired t-test should do the trick.

I agree that the first thing to do is to make sure your measurements were correct, i.e. you took into account the possible saturation and normalized for the background. Ideally, you would also try several different loadings to correct for the non-linearity of signal but it might by just a subtlety.

After this, normalization for the control is a good thing, given that your measurements came from three different blots.

You then proceed with a paired t-test, as recommended, which will give the highest power among all other alternatives. In theory, for this you need to assume that your samples came from a distribution close to a Gaussian. Well, you cannot be sure. Unfortunately, normality tests are not going to help because of a too low n. Fortunately, the central limit theorem allows you to use tests like Student's even if the distribution is not quite Gaussian. So the paired t-test should work alright anyway. Do not use non-parametric tests: they have too little power in this range of n!

There is one more complication: t-tests assume that the SDs are the same in both populations compared. Quite unluckily, your normalization to the control makes SD of the control population artificially equal 0. That's a bad thing. It basically shows that the best experimental set-up in your case is to run all your samples on the same blot and read normalized signals all together. This will enable you to omit normalization to the control, restore proper SDs and make the whole thing reliably analysable.

Thanks a lot

If I perform a paired t test with my normalised control (since my standard deviation is zero) do u think my results are still acceptable?

Although it is not the cleanest way to do this... yes! The paired t-test with equal n's in each group will stay pretty robust even if SDs are unequal.

Thanks

I think that un paired t test is the best. People should check again the definition and the setup for a paired an unpaired test. http://graphpad.com/guides/prism/5/user-guide/prism5help.html?stat_how_to_ttest_paired.htm.

As Subhadeep said, the best way would be to run all samples together. If this, for whatever reason, is impossible, we need to deal with the proposed set-up. The use of an unpaired t-test will impact dramatically the power. On the contrary, the paired t-test, having a higher power, has a good justification, too: the controls and the cases are effectively PAIRED since they come from the same blot. This makes them directly comparable. I also suspect that they were prepared in parallel as well, were not they?

both control and mutant came from same blot. And samples were also prepared in parallel.

I suppose you have the same trend in every experiment. You normalise your control, and this group therefore no longer has any variability. A more pragmatic statement therefore would be that a statistical analysis is not even required. There is no uncertainty that your signal increases.

On another note I agree with Subhadeep on running the samples together on one gel. Or, alternatively, to run three lanes for each sample from a single experiment on one gel. That would allow you to assess technical variabilty and will provide you with an uncertainty measurement for your mean-normalised controls.

Everyone must keep in mind that Western blot is NOT a quantitative technique and too make it such would require controlling every step of the method and ensuring that Ab:Ag interactions and ECL reactions are in the linear range. My advice, just show the gels and if you need to use graphs to show effects then the effects are probably not that biologically relevant. Or alternatively use a quantitative method such as FACS or ELISA.

We routinely use immunoblotting for absolute quantification of protein levels in cell lines and clinical samples at nM accuracy. Appropriate controls provided, nothing speaks against quantiative immunoblotting as a reliable readout. The major advance is really made on the detection side, with high dynamic range sensitive CCD systems providing enormous benefits over old-school film-based detection. Titrations of purified protein give excellent correlations over a wide range of intensitites. Related to this, high-throughput techniques such as RPPA have been developed and are now beginning to be more widely used in clinical/translational studies. In your case, Nitha, a relative quantification is absolutely fine to demonstrate a trend. I'd take Derek's statement that "if you need to use graphs to show effects then the effects are probably not that biologically relevant" with a bit of scepticism. Many biological processes are highly non-linear. As such, small changes in the right critical components of a signaling network can make huge differences. This can for example be found in ultra-sensitive signaling components or molecular rheostats that are working close to thresholds of decision switches.

Even with CDD systems for most labs (perhaps Markus' lab is an exception) it is a tough ask to control the vast number of variables with immunoblotting required to make it into a fully quantitative technique and one can argue that with so many other better ways to do this including mass spec, ELISA, FACS etc why bother? I agree with Markus that it is questionable as to what level of increase/decrease in expression of a protein becomes biologically significant, however when one drops below say 2-fold difference detected using a western blot it becomes tough to argue on this basis alone that one has a physiologically relevant effect unless taking into account changes in the expression of other functionally linked molecules - again this argues for more quantitative methods and with a systems biology approach.

Hi Nitha,

Though this approach is not very accurate, but an acceptable way to analyze data (in qualitative manner) between control and experimental groups by western blots. I will use the value “normalized to the 1 (1 and 3.85) for analysis” and for statistical analysis, I will use unpaired t test. It is wise to run both control and mutant on same blot, and prepare them in parallel. And you have done it.

Another option you have is to run all your independent biological replicates in the same gel (if you only have two samples per experiment and three experiments, you can run all six samples). In this way you make sure to use the same exposure for all replicates, and then perform the appropiate statistical analysis. The advantage is that for control, SD is no longer cero, since you can normalize each sample to actin in the same picture, and obtain the average and SD without exposure issues. Find attached an example done with biological duplicates. Good luck.

Quantitative Western-blotting is fraught with problems, not least because densitometric signals E depend on antigen concentration m in an exponential manner: E = a m^b. Hence the ratio E1/E2 = m1^b / m2^b and you need standard curves even for relative determinations. In addition, the exponent b varies from gel to gel, so all samples need to be run on the same gel (Pitre et al., Anal. Biochem. 361 (2007) 305-7).

However, once you determined that your antibody binds only to the protein of interest, you do not need to western blot for quantitation. A simple dot-blot suffices. For such experiments I use a 96-well filtration manifold to spot samples onto a PVDF membrane. This spreads all samples onto spots of identical shape and size. Then develop the membrane like for a western, with chemoluminescence detection in a 96-well luminometer, using an home-made holder for the membrane. It is very easy to run concentration standards in this system, verifying the relationship between signal and antigen-amount. For my application, I found that relationship to be linear over 5 orders of magnitude! Just two hints:

-The filtration manifold should have a silicon gasket to seal the membrane to the manifold. Some simple systems use only filter paper, these do not work reliably.

- Nitrocellulose bind proteins with lower affinity and capacity than PVDF and does not work well in this application.

From my experience, I completely agree with Dr. Derek Mann. Westerns are not quantitative. You can compare only proteins on the same gel. Actin, ANT and some other proteins, which are often used as a loading control , vary significantly both between species and the organs within the same animal. The other important issue: Enzymes may have different activities, and lower content does not mean lower activity. If a protein greatly increased after your treatment, it does not mean that the function also increased. On the contrary, there are many examples when an increase in expression and even in the amount of protein speaks that this function does not work and the body (or cell) tries to overcome the lack of the function by increasing expression of the protein. The most stunning example is with the ANT1 knockout mice. Lack of oxidative phosphorylation, due to the absence of ANT, resulted in tremendous activation of the synthesis of new mitochondria, but they are all dysfunctional. So, think twice before performing "quantitative" Westerns.

Firstly, I like the fact that this is becoming an interesting methodological exchange, now obviously deviating from the original stats-related question. I hope the original poster doesn't mind.

The issue that Engelbert brought up is indeed a point to consider for film-based detection, in which one would need to take into that simplification to a linear relationship might hamper the analysis due to the non-linearity implicated in the methodology (refer to Lambert-Beer's law for further detail). This problem does not apply for CCD-based detections with digital cameras. Another point is the digitization of the actual film, which is commonly done by simple scanning (a lot can go wrong there due to poorly adjusted scan procedures and (often) lack of transmission illumination). Also, the dynamic range of a film is rather poor and some signals are easily saturated while weaker signals cannot be detected yet. Finally, 'densitometry softwares" are often 'black boxes' in a sense that the actual procedure to determine intensities is not obvious. I have personally seen softwares that are clearly providing scewed semi-automated outputs when compared to softwares that allow proper control of the indvidual steps. For example, to me it seems unclear even in the Pitre et al. paper cited above how this was done. While their points are valid, they neither show any of their (supposedly 8 bit) immunoblotting signals for demonstration and do not (or cannot) disclose how the software they used measures the signals.

Also Alexander's comment is important, since it indeed makes no sense to compare signals from different membranes or to do loading corrections across different tissues. In the latter case, user accuracy in gel loading needs to suffice.

Normalising the ratios is the best way to average out the sample data. Following this since you are only comparing two data points (WT and mutant) student t test is fine.

Dr Ying-Xin Fan has identified all of the variables that concern myself when using WB for protein quantification.

Most important things have been said already,and all contributors have a point. However, one other thing might be useful to consider: with Ying-Xin's reservations in mind, one needs the experiment repeated three times in order to obtain four measures per band. Take away the inevitable aberrant value, and average the remaining three. Obviously, the values are all normalized to the loading control. CCD-based quantification is definitely preferred over scanning bands, but WB remains the poorest method for quantification and should be done with utmost care when other assays are not an option.

One way to make sure that you can quantify the results of an immunoblot is to run several loads of the sample to ensure that a plot of intensity of band of interest vs the load is linear. Doing this instead of running triplicates of the same load, you will use less of your experimental sample and check on the linearity at the same time. If there are not enough lanes on the gel to do this and different samples have to go on different gels/blots, save a few lanes to run aliquots of the exact same samples. Even if you develop the blots simultaneously, there will be variations, so the uniform load of the same sample on every blot will give you a way to normalize across blots.

Excellent comment, Anna.

I agree with comments above that appropriate experimental replicates and internal controls need to be used. A dilution series is a good idea.

Rather than using ECL based detection I would rather use the IR dyes (infrared) and a LI-COR scanner if you have these available.

http://www.licor.com/bio/applications/quantitativeWesternBlots/introduction.jsp

This detection method should give a linear readout.

I do not recommend trying to do quantification on WB as this is a very semi-quantitative method.

Quite often, researchers try to apply statistics to western blots by initially quantifying by densitometry and then applying statistics to the numbers obtained. I would suggest that you simply describe your findings in terms of "more" or "less" signal rather trying to reach statistical significance.

Since the statistical tests required n=30 and often equal variances of the two sample populations in the first place, you will be far from fulfilling the statistical test requirements. I will be safer and sounder to just describe what you observe and illustrate your point with a blot rather than attempting to do densitometry as is sometimes done.

Jean-Charles

Agree with Neel Jean-Charles. Western blot is semi-quantitative. Quantification is meaningful only if you can establish that you are working in the linear range. This requires careful titration of antigen, primary and secondary antibody for each antigen detected. Best is to have a standard on the same blot. The same requirement applies whether your are using HRP or fluorescence labeled antibodies, films or CCD detectors.

I agree with Anna Tan-Wilson and Neel Jean-Charles and want to add that, even if you are working in the linear range, the intensity of the band is not exactly proportional to the amount of antigen on the membrane. I mean, the double in the intensity of the signal not necessarily reflects the double amount of antigen: it means more, maybe less than twice, maybe twice or maybe more than twice. That is because the linear graph obtained not always has a slope =1, the slope varies among combinations of antigen-primary antibody-secondary antibody, etc. It should be determined in every case.

Just to correct the math: it is not because of the slope, it is the intersept which differs from 0. In other words, 0 signal does not mean 0 antigen.

Yes Alexander, you are right. Then it is both because the slope rarely equals 1. I have probed it myself by performing WB with serial dilutions of one sample (unfortunately not with purified and quantified antigen) and plotting the results.

Maria is right that signal may not be exactly proportional to amount of antigen. Other factors (such as amplification caused by enzymatic detection with HRP, substrate availability/depletion, local saturation of membrane-binding capacity, transfer variability, etc) can influence signal intensity. A high-abundance sample with a lot of target protein may experience transfer and detection differently than a low-abundance sample with very little target.

For semi-quantitative Westerns, it is absolutely critical to operate within the linear dynamic range of your detection method. I also think it's very important to evaluate the intra-blot and inter-blot variability to know if the differences you are seeing exceed the error of the method.

For María Mediavilla: It is not both. Alexander was right - it is the intercept only (which can be at least partially solved with proper background subtraction, however). The slope does alter the proportionality (as long as it is >0, of course). Anyway, the slope is relative, depending on the units (grams or miligrams vs. units of fluorescence or intensity). Elementary math...

The original question:

Although the quantification and statistical analysis of WB experiments is not easy and inaccurate, I do not think that showing just one "representative" WB is the best choice. I never did an absolute quantification with purified protein standards, as I always counted with a fold increase/decrease over a control (e.g. non-treated cells or cells with maximal response) run on the same WB.

My way:

1. I run all samples (including the control of NT cells) to be compared on a single gel/membrane. I always try to have the same loading (cell number of amount of total protein).

2. I always probe the membrane for the specific protein (or phospho-protein) and a loading control (e.g. GAPDH).

3. I quantify the signals by Odyssey IR system (it give better results than an enzymatic reaction).

4. For the quantification, I use Aida SW or ImageJ. I always subtract background, although it is difficult sometimes (non-specifities).

5. I normalize signals from my specific antibody to the signals from the respective loading controls.

6. I use the numbers from (5) to calculate the fold increase/decrease over the control (non-treated sample). This number is a mere estimate, but the best estimate I can get.

7. I put results from several (usually 4 or more) independent experiments together, calculate the mean, SD, and use Ttest without the assumption of equal variances (Welsch's correction, even MS Excel knows it).

I know than n is too small to run a non-parametric test or check for normality, but I am convinced that this is better than nothing. It shows at least that the experiment was done more than once with reproducible results. People tend to be biased and to show one "representative" experiment that is not representative at all (it is the very best experiment they have to support their conclusion).

Dear Ondrej Stepanek,

I still must defend my point here. I do not argue against proportionality (if you are working in the linear range and after subtracting the background). Yet, you must translate the amount in signal change to the change in the amount of load of epitope on the membrane. This could be done by using your linear plot (or its mathematical function) and calculate it. But many researchers just use the signal intensity as equal to the protein of interest level.

That is what I am saying.

Yes, Ying-Xin Fan I agree with you.

Anyway, I have realized that Ondrej and Alexander are right... my math was wrong.

Sorry about that.

Western Blot and the statistics are both a big tools, in my opinion pretty separated, I don't suggest to use the hammer to screw in...

I allow to my self to say to my students about WB film:

- We observe weak/significant/strong/ like a hell increase of the protein content

- There is 2ml shift in the size-exclusion separation

- 2mm difference in the band position on the SDS-PAGE can suggest the protein is modified or degraded

- out of set of the films in the range 5s-30min of ECL exposure, I'll pick up the one will show you 3x increase, or 1.2x increase, or 10x increase of your protein content, depending what fits your theory...

Sorry dear Ying-Xin Fan, you said exactly what I meant, but wrote it with my sense of humor caused misunderstanding. The picture is showing the results of human samples with commercial specific AB (was not specific at all, we validated with the four another ABs), anti-goat is also showing a nice bands... There is an comparison of short/long expo of the experiment we know was an artifact with many interesting bands. This is showing how careful should we be with withdrawing the conclusions in the science what you meant as I understood. With crazy hypothesis possible to verify by reproducible techniques I let the students feel free...

Have you read about Nature's new standards for data analysis? They will be requiring more info about controls, data analysis methods, technical variability and reproducibility. I hope this new trend will make the methods more transparent, so you can more easily evaluate how the authors reached their conclusions. Quantitative Westerns are a great tool, if you're careful to avoid misinterpretation (or over-interpretation).

Thanks everybody for thoughtful comments/suggestions. While many critical aspects of the WB quantification have already been addressed in detail, I just wanted to bring to everybody's attention the aspect of the membrane "stripping", the technique frequently used to re-probe the same membrane(s) with the "loading" control antibodies or even with different set of primary/secondary antibodies. In our hands the membrane stripping always has some "negative" effects on the signal quality and intensity, therefore we try to avoid this approach at any costs. With this in mind the statistical analysis of the WB signals becomes even more complex and subjective...Dr. Piwowarski's WB image is a perfect example what can happen to the WB signal following a single technical variance (e.g. extending the exposure time).

Regards

Stripping is also a big concern to me, but for slightly different reasons. This process causes protein loss from the membrane, probably in a non-uniform, sequence-specific manner. Unfortunately, this means that the relative protein levels after stripping are not exactly the same as the relative protein levels before stripping. Since we don't know which proteins are most affected, we can't correct for this. My rule is to consider stripped blots as qualitative data only. If you need to normalize and get maximum accuracy, use multiplexed fluorescence to detect both proteins at the same time on the same blot.

Dr Xianfeng Wang asked an essential question:

https://www.researchgate.net/post/How_do_you_choose_a_good_antibody_for_western_blot

I'strongly advice all of you to follow this topic!

Please check this link

http://www.lukemiller.org/journal/2007/08/quantifying-western-blots-without.html

The loss of the protein depends on the stripping method. We do stripping using water and NaOH solution at RT (10 min in H2O, 10 min in 0.2M NaOH, 10 min in H2O), so it is not very strong stripping method but OK one. For a few antibodies we had to try what was better: to use the specific antibody first (before stripping) or antibody for the housekeeping protein (tubulin or actin). And we have seen no significant differences in the right bands, just some additional non-specific bands with some antibodies, when they were used on stripped and re-blotted membranes. However, we usually do stripping only when the protein is too close to the housekeeping protein for the cutting of the blots to be feasible. But it is just because of the additional non-specific staining after re-blotting not because any protein is lost from the blot.

Dear Nitha,

Western blot quantification is always a big concern. It's quite complicated to average values obtained from samples loaded in different electrophoretic runs, because of differences (even small) in the exposition time during the chemioluminescence detection, in the binding of the antibody etc etc. Thus, in my opinion it is not properly correct to apply statistical analyses on these data. Is it possible for you to load all the samples (both Wild type and mutant samples) you need to average on the same gel?

As Prof. Gediminas Cepinskas I hate stripping. Instead I suggest to plan the blot and ABs in order to slice it in 1.5 cm horizontal strips. Gradient gel, Ponceau-S staining of the blot and you can develop out of one sample/gel 4 westerns detecting the proteins of the mass of 200, 120, 80, 30 kDa respectively. You incubate the strips in parallel, develop as well doing the same job, like for one antibody only.

In our lab we use Multistrip western blotting for quantitative analysis. It is a modified immunoblotting procedure based on simultaneous electrophoretic transfer of proteins from multiple strips of polyacrylamide gels to a single membrane sheet. In comparison with the conventional technique, Multistrip western blotting increases the data output per single blotting cycle up to tenfold, allows concurrent monitoring of up to nine different proteins from the same loading of the sample, and substantially improves the data accuracy by reducing immunoblotting-derived signal errors. This approach enables statistically reliable comparison of different or repeated sets of data, see details in:

http://www.ncbi.nlm.nih.gov/pubmed/19378054

I agree with all concerns about western blot quantification. I think that a western blot should be repeated at least 5 times with the same set of samples to be reliable. If the difference is real it should holds up with only some variability in the magnitude.

Hi

All answer is correct. As you know western blot is a quality test, it has been difficult to change the result as quantity. But you can use densitometry program, measure the density of your western blot bands and relatively compare them.

I found this discussion since I'm trying to convince a biologists to do things my way. I find Ru-Jeng Teng has the answer I recommend, mostly.

Call dividing protein of interest by house-keeping protein "normalizing". Call dividing by the control condition in each experiment "adjusting", so as not to confuse it with the first normalizing. As a first example assume there are several conditions of interest, and multiple replicate "experiments" that measure them. (That is not the only possible design.) That is I am assuming the measures are paired in a sense (in the same experiment).

If there are just two conditions of interest, paired T-test is fine, and whether you adjust the data is irrelevant then. Model (whether there are two treatments or more) is a two-way ANOVA model.

Yij = Ai +Bj +Eij where i=1,2...I are the conditions and j=1,2,...J are the experiments, and the sum of the Bj add up to zero. There are I*J - I - (J-1) degrees of freedom in the denominator of the test. The estimate of the Bj's are the sum of Yij for experiment j minus the sum of all the Yij. Note how that is not quite the same thing as "adjusting to the control". You could compute Zij = Yij - Bj (where Bj are the estimates) and think of them as the data after it's been adjusted for experiment effects, and plot those means and standard deviations, but must say "after experiment effects have been removed". There would be a standard deviation for the control condition. It would be good if you showed the raw data in a supplementary figure or table.

Adjusting experiments, and then using two-sample T-tests (or ANOVAs that do not model the experiments) is essentially cheating for the set-up above. It is because you fanatasize you are using the model Yij = Ai +Eij, and count that there are I*J - I degrees of freedom in the denominator of the test, ignoring that you used the equivalent of J-1 pieces of data (parameters) to do the adjustment. You are failing to penalize yourself for having already used some of the data. Perhaps some people think two-sample test (or anova without experiment effects) is good is because it can give a smaller p-value, cause it is cheating in a way that gives it an edge ("P-hacking"). The other reason is that they don't know how to fit two-way ANOVA models. Both are bad reasons, not good ones.

To repeat, you do not need to "adjust" data if you use the two-way model above. The Yij are simply the ratio (after normalizing to actin or whatever). I would suggest you take logs like Ru-Jeng says. Do you think that if standard deviations for protein P are 5 units (without logs) in group A, that they will also be 5 units in group B where it is 10 times more abundant on average, or do you think the percent variation might be more similar? Taking logs tends to "stabilize the variance". After base 2 logs, everything is in units of doublings. It helps with right skew too. I've seen people weigh 500 lb, perhaps 320 more than average (say average is 180 - I'm making it up), but I have never seen one weigh 320 lb less than 180 lb. If it's an abundance, I take logs almost always (e.g. tumor weight, number of cells, estimated mRNA from array or PCR).

You could run a different design, where I have 5 plates of each of three (say) conditions, and the 5 plates for a condition have no particular order, but are all done at the same time (perhaps randomized location, randomized lane on the gel). We say "the replicate plates are exchangeable". I'd normalize to actin (or whatever) and fit the model Yij = Ai + Eij again, there is no need to adjust. i=1,2,3 are the conditions. Of course I'd take logs first. If there are just two conditions it's a two-sample T-test, if three or more it's a 1-way ANOVA model.

I said something wrong yesterday, about adjusting not mattering if you fit the proper anova models. That's only true if you take logs first (and adjusting is then subtracting rather than dividing by the control condition). If you don't take logs, and divide by the control, you can get a different p-value. For example pairs of normalized data that go 1, 2, 3 for controls, and 10, 22, 29 for treateds gives =.066 for paired T-test. If I adjust the data first (by dividing rather than subtracting the control values) data becomes 1, 1, 1, and 10, 11, 9.66667. P-value for paired T-test is now .00188. If I adjust by subtracting control value instead, p is still .066.

PS: If I take logs first, I get p=.00028 for paired T-test, whether I adjust by subtracting (log-transformed) control values or not. I find that comforting.

Thanks for the contributions. very helpful.